Abstract

Abstract We study whether the solvency problems of Spain's weakest banks in the Great Recession have caused employment losses outside the financial sector. Our analysis focuses on the set of banks that were bailed out by the Spanish authorities. Data from the credit register of the Bank of Spain indicate that these banks curtailed lending well in advance of their bailout. We show the existence of a credit supply shock, controlling for unobserved heterogeneity through firm fixed effects, and assess its impact on employment. To this aim, we compare the changes in employment between 2006 and 2010 at client firms of weak banks to those at comparable firms with no significant precrisis relationship to weak banks. Our estimates imply that around 24% of job losses at firms attached to weak banks in our sample are due to this exposure. This accounts for one-half of the employment losses at firms that survived and one-third of employment losses at those that closed down. 1. Introduction Do shocks to the banking system have real effects and, if so, do they cause job losses outside the financial sector? Both questions have strongly resurfaced in the wake of the economic and financial crisis that started in 2008. The renewed interest in the real effects of credit supply shocks is motivated by the exceptionally strong and persistent contraction of economic activity in the countries that suffered a banking crisis, like the United States and several peripheral countries in Europe. In this study, we use data from the credit register of the Bank of Spain to analyze the link between the unprecedented drops in bank lending and employment in Spain. Our identification strategy exploits large differences in bank health observed at the onset of the crisis. The entire banking sector suffered the consequences of the collapse of the construction sector and the bursting of a housing bubble, and most banks were cut off from wholesale funding for a while, but the main problems were concentrated in savings banks (cajas de ahorros). We focus our attention on the ones that were bailed out by the Spanish government as part of a large-scale restructuring process that involved 32 savings banks and one commercial bank. We show that this set of weak banks started to curtail lending relative to the other banks almost 2 years ahead of the bailout process. Our main objective is to explore how this credit supply shock affected employment growth in 2006–2010 at the firms that maintained a precrisis relationship with any of these weak banks. The Spanish economy provides an ideal setting to analyze this issue. Spanish firms are more reliant on bank credit than their counterparts in most advanced economies. In 2006, the stock of loans from credit institutions to nonfinancial corporations represented 86% of GDP compared to 62% in the European Union (European Central Bank (ECB) 2010). On the contrary, funding through financial markets is rarely used: on average only five large corporations per year issued publicly traded debt between 2002 and 2010, and the number of companies listed in the stock market is tiny. Finally, the vast majority of firms in Spain are small- and medium-sized enterprises (SMEs), and many of them became highly leveraged prior to the recession. We are obviously not the first to estimate the real effects of credit supply shocks. A number of recent studies have demonstrated the adverse impact of such shocks on employment and investment (see Section 2). Most of this work is however based on either incomplete data on bank loans to the corporate sector—such as syndicated loans—or information about banking relationships rather than loans. One of the main contributions of our study is to use a comprehensive data set that includes loan-level data. The credit register of the Bank of Spain provides exhaustive information about all bank loans to firms in the nonfinancial sector, and these data are matched to balance sheet data for all banks and nearly 150,000 firms. We are thus able to trace all credit flows to a large sample of firms, for which we also have information on their credit history, such as loan defaults, and their applications for the first loan from other banks. Hence, we observe credit demand by firms that apparently need to establish a new banking relationship, and the data from the credit register allow us to determine whether the loan application was granted or not. Our high-quality data let us perform more tests than related studies carry out and explore the presence of heterogeneous effects along many dimensions, but above all they allow us to resolve several key identification issues. The first challenge is the need to disentangle changes in credit supply from concurrent changes in credit demand. Between 2007 and 2009, the ECB Bank lending survey indices for Spain show a simultaneous increase of around 40% in the bank lending standards applied to nonfinancial firms and a similarly sized drop in their loan demand (Banco de España 2015). To obtain clean identification of the credit supply shock, we use the standard procedure of Khwaja and Mian (2008) to analyze credit growth at the bank-firm level. The results clearly demonstrate that weak banks curtailed credit vis-à-vis healthy banks that lent to the same firm. Thus, controlling for firm fixed effects, we show that there was indeed a differential credit supply shock. Moreover, we also establish that the affected firms could not find new lenders to fully compensate this reduction in credit supply, which implies that the impact found at the bank-firm level was partially transmitted to the level of the firm. Finally, when we analyze employment growth we find that these firm-level credit shocks caused relatively large employment losses at firms with a precrisis relationship to weak banks. To capture these shocks, our baseline difference-in-differences (DD) specification includes a dummy variable for firms with a weak-bank loan-to-asset ratio above a minimum threshold. The second main challenge is to control for selection effects. Before the crisis, healthy banks may have worked with better firms than weak banks, as indicated by differences in the observable characteristics between firms above and below the threshold for the weak-bank loan-to-asset ratio. Failing to control for these differences would bias our estimates upwards if the firms above the threshold suffered a stronger contraction of demand or if they were more vulnerable to reductions in the availability of credit than the firms below the threshold. Moreover, selection may also occur on unobservables and in this case the introduction of firm controls need not suffice to avoid the bias. As already indicated, in the analysis of credit growth at the bank-firm level this problem is dealt with by introducing firm fixed effects. Moreover, we also estimate a firm-level specification in which the fixed effects are replaced by firm control variables. This DD specification in growth rates includes exhaustive controls for differential trends in credit growth by firm characteristics and it includes a full set of fixed effects by industry-municipality pairs to control for local demand effects. The resulting estimate of the impact of weak-bank attachment on credit growth is virtually identical to the one obtained in the within-firm specification. This reveals that unobservables do not play a significant role as far as access to credit is concerned, but they could still generate different patterns of employment growth. In our analysis of the impact of weak-bank attachment on firm-level employment, we perform several tests to deal with the potential problem of selection on unobservables. First, we show, using the normalized difference test of Imbens and Wooldridge (2009), that selection on observables is not that important, because firms attached to weak banks only differ significantly from the rest in 3 of the 14 controls that we use: they have a lower capital-to-assets ratio, a higher debt ratio, and they work with more banks. In addition, we estimate a panel fixed-effects model with yearly observations for employment growth and we use matching techniques to directly compare firms within narrowly defined cells. In neither case do we find any significant difference with our baseline. We nevertheless also apply the procedure in Oster (2017) to place an upper bound on the impact of unobservables on our coefficient of interest. Lastly, we exploit a legal change in the regulation of savings banks in December 1988 to construct an instrument that generates exogenous variation in weak-bank attachment. The results of this instrumental variable model must be interpreted with caution, as explained in what follows, but they confirm that weak-bank attachment exerted a significant negative effect on employment growth. In the rest of the analysis, we consider several extensions of our baseline setup to analyze the transmission mechanism of the credit shock and to explore the role of firms’ financial vulnerability. We start by estimating a separate effect of weak-bank attachment on credit lines, finding that weak banks strongly reduced access to credit lines relative to healthy banks. A direct impact of working capital on employment therefore seems to prevail over potential indirect effects via reduced investment. Furthermore, we offer a novel decomposition of job losses through adjustments along the internal and external margins, and we estimate the effect of weak-bank attachment on changes in the wage bill and in the share of employees with a temporary contract. To the best of our knowledge, we are the first to offer a comprehensive analysis of these margins of adjustment. Lastly, we interact the treatment variable with an extensive set of firm characteristics that capture different dimensions of firms’ financial vulnerability. Our baseline result is that weak-bank attachment caused employment losses of about 2.8 percentage points (pp). This estimate is large, accounting for 24.4% of the total fall in employment among exposed firms in our sample. Surviving firms account for about one-half of the overall loss, whereas the remaining half corresponds to job losses in exiting firms. Nonetheless, weak-bank exposure explains a larger share of job losses in downsizing firms than in exiting firms (around one-half vs. one-third, respectively), and we show that temporary employees bore the brunt of the employment adjustment. Lastly, we find that financially vulnerable firms suffered the largest job losses. The rest of the paper is organized as follows. In Section 2, we review previous empirical work on the topic, and in Section 3 we provide background information on the Spanish economy before and during the financial crisis. Section 4 describes our data, and Section 5 presents our empirical strategy. In Section 6, we show our estimates of the effect of weak-bank attachment on credit growth, and in Section 7 our baseline employment effect estimates. Selection effects are dealt with in Section 8, and Section 9 presents results on treatment heterogeneity. Various margins of adjustment are studied in Section 10. Section 11 contains our conclusions. Two appendices provide information on weak banks and securitization, as well as details on the variables used. 2. Literature Review In recent years, there has been a surge of studies exploiting quasi-experimental techniques to estimate the real effects of credit supply shocks.1 The closest ones are the seminal contribution of Chodorow-Reich (2014) and the article by Greenstone, Mas, and Nguyen (2014).2 Both studies exploit cross-sectional differences in lender health at the onset of the recent crisis to study the link between credit supply shocks and employment. In Greenstone et al. (2014), this link is indirect, as they do not have access to loan-level data or information about firms’ banking relationships. To circumvent this problem, they construct a county-level credit supply shock from the product of the change in US banks’ small-business lending at the national level and their predetermined credit market share at the county level. Using confidential data from the Bureau of Labor Statistics Longitudinal Database (LBD), they find that this measure predicts the reduction in county-level credit to small, standalone firms, and their employment levels over 2008–2009. But even assuming that the entire reduction in lending is due to a drop in credit supply, the estimated effect is small, around 5% of the employment fall. Chodorow-Reich (2014) does have access to loan-level data from the Dealscan syndicated loan database. He constructs a firm-specific credit supply shock that is equal to the weighted average of the reduction in lending that the firm's last precrisis syndicate imposes on other firms during the crisis. These data are matched to employment records from the LBD data set for a sample of just over 2,000 firms. In line with Greenstone et al. (2014), he finds that SMEs with precrisis relationships with less healthy banks faced stronger credit constraints after the fall of Lehman Brothers and reduced their employment more compared to clients of healthier banks, attributing between one-third and one-half of job losses in SMEs to this factor. By contrast, there are no significant effects for the largest companies in the sample. In this paper, we also exploit differences in lender health to uncover the employment effects of credit supply shocks, but the access to credit register data represents a substantial improvement on the existing work in this field. First, we are able to reconstruct the entire banking history of firms and to trace back all credit flows and not only syndicated loans.3 Second, the representative nature of our large sample of firms is important to gauge the overall effect of the credit shock on employment. Studies relying on data for relatively large firms may substantially underestimate the impact of credit shocks if larger firms are more able to find substitutes for bank credit than smaller firms. We do not find compelling evidence of such differences by firm size, but in other countries they may be important when large firms have access to well-developed markets for private debt. Third, access to detailed micro data allows us to perform a wider range of robustness checks and to explore the presence of heterogeneous effects along more dimensions than most existing studies. Our analysis pays particular attention to the role of firms’ financial vulnerability. Apart from standard indicators, such as firm size or age, our analysis also includes controls for firms’ degree of bank dependence, the term structure of their bank debt, and their credit history. This analysis reveals that a bad credit history in the form of past defaults triples the negative effects associated with a precrisis relationship with a weak bank and these effects come on top of the almost 20 pp reduction in credit growth for all firms with a bad credit history. Similarly, for bank-dependent firms with a ratio of bank debt to total debt above the median, job losses are five times bigger than the average treatment effect. These strong differences in the intensity of the effects confirm the finding in Paravisini et al. (2015) that it is key to compare firms within very narrowly defined cells to avoid omitted variable bias. The theoretical literature has identified several potential transmission mechanisms through which shocks to the banking system might affect employment in nonfinancial firms (see the review in Boeri et al. 2013). First, mismatch between the timing of payments to workers and the generation of cash flow may force firms to finance salaries as part of their working capital. Second, turnover costs in the labor market transform labor into a quasi-fixed factor of production, creating a link between employment and external finance that is similar to the well-known link with investment. Third, financial frictions may alter the optimal mix of permanent and temporary jobs, as the latter are cheaper to destroy, and this may in turn have important implications for the cyclical volatility of employment. Lastly, the availability of external finance may indirectly alter the use of labor if capital and labor are complements in production.4 Although we cannot identify the relevance of these mechanisms, we try to shed some light on them in several ways. On one hand, we explore the relative importance of weak-bank attachment on short-term funding, which indirectly informs us about the purpose of the loans. Next, we consider three alternative margins of employment adjustment. First, we offer a decomposition of job losses along the internal and external margins, showing that weak-bank attachment leads to a significant increase in firms’ exit probability. This finding helps to understand the persistence of the effects of credit shocks, because it is cheaper and quicker to create jobs at ongoing businesses than to rebuild firms once the economy recovers. And second, for the sample of surviving firms we estimate the effect of weak-bank attachment on the size of the wage bill and the share of temporary jobs. Popov and Rocholl (2016) and Fernandes and Ferreira (2017) offer comparable results on the importance of wage cuts and changes in the composition of employment, respectively, but we are the first to consider all three margins jointly. 3. The Financial Crisis in Spain The Spanish economy experienced a severe credit crunch in the Great Recession. In this section, we briefly document the magnitude of this credit crunch, but we start by defining the set of weak banks, so that we can compare the evolution of lending by weak and healthy banks. 3.1. The Bank Restructuring Process During our sample period, the Spanish Government intervened a total of 33 banks (see Table A.1). First, two small banks were nationalized and quickly resold. Later on, the Government fostered either bank mergers (26 weak banks) or the takeover of ailing banks by other banks (5 banks). Most of these operations entailed State support, in the amount of 11.6 bn euro, i.e., about 1.1% of Spanish GDP (Banco de España 2014). We classify a bank as weak if it was nationalized, it participated in a merger with State funding support or it was insolvent and bought by another bank. Banks that absorbed other banks are considered to be healthy. During our sample period, all weak banks except the two small nationalized ones were run by their incumbent managers and all the institutions participating in mergers remained separate legal entities. Further, consolidation operations and the bulk of the nationalizations took place in 2011–2012 (see Appendix A and International Monetary Fund 2012), and savings banks were forced to convert into commercial banks. These operations fall outside the scope of our analysis and the same is true for the recapitalization of the banking sector that took place in 2012 with financial assistance from the European Financial Stability Facility. Finally, it is important to stress that savings banks were subject to the same regulation and supervision by the Bank of Spain as commercial banks, though they had a different ownership and governance structure. Not being listed in the stock market, they were less exposed to market discipline than commercial banks but also quite limited in their ability to raise capital in response to the crisis. Furthermore, they were de facto controlled by regional governments, which led to delays in their restructuring and may have affected their credit allocation prior to the crisis.5 3.2. The Differences in Lender Health Table 1 illustrates the differences in lender health at the onset of the crisis. In the last two columns, we report the t-statistic and the normalized difference test of Imbens and Wooldridge (2009), for which Imbens and Rubin (2015) suggest a heuristic threshold of 0.25.6 Both tests yield the same results. In 2006, weak banks were on average larger than healthy banks and held less capital and liquid assets. By contrast, both their rate of return on assets and their share of nonperforming loans were comparable, but this apparent similarity hides latent losses at weak banks, which surfaced later, as witnessed by their vastly larger ratio of nonperforming loans in 2012.7 The ratio of securitized loans to assets is also larger for weak banks, but not significantly so, suggesting that it was not key in explaining the differential evolution of credit during the crisis between the two sets of banks. In what follows, we conjecture that the comparatively large share of loans to construction companies and real estate developers—henceforth real estate industry or REI—is a key source of the surge in loan nonperformance and the comparatively strong contraction of lending by weak banks. Loans to the REI make up 68% of all loans of weak banks to nonfinancial firms compared to 37% for healthy banks. Table 1. Descriptive statistics of healthy and weak banks (2006). Healthy banks Weak banks Mean St. dev. Mean St. dev. Mean t test Normalized difference ln(assets) 13.7 2.1 16.4 1.0 7.1 1.14 Own funds/assets 8.4 9.0 5.2 1.2 $$-$$2.0 $$-$$0.35 Liquidity/assets 23.7 22.4 11.5 4.5 $$-$$3.1 $$-$$0.54 Return on assets 1.0 1.7 0.9 0.3 $$-$$0.5 $$-$$0.09 Nonperforming loans 1.5 6.3 0.7 0.6 $$-$$0.7 $$-$$0.13 Nonperforming loans (2012) 8.6 12.7 22.0 6.0 3.5 0.95 Loans to REI/loans to NFF 36.8 22.3 67.9 8.1 7.9 1.31 Securitized loans/assets 14.9 10.5 18.5 6.3 1.6 0.30 Healthy banks Weak banks Mean St. dev. Mean St. dev. Mean t test Normalized difference ln(assets) 13.7 2.1 16.4 1.0 7.1 1.14 Own funds/assets 8.4 9.0 5.2 1.2 $$-$$2.0 $$-$$0.35 Liquidity/assets 23.7 22.4 11.5 4.5 $$-$$3.1 $$-$$0.54 Return on assets 1.0 1.7 0.9 0.3 $$-$$0.5 $$-$$0.09 Nonperforming loans 1.5 6.3 0.7 0.6 $$-$$0.7 $$-$$0.13 Nonperforming loans (2012) 8.6 12.7 22.0 6.0 3.5 0.95 Loans to REI/loans to NFF 36.8 22.3 67.9 8.1 7.9 1.31 Securitized loans/assets 14.9 10.5 18.5 6.3 1.6 0.30 Notes: There are 206 healthy and 33 weak banks. Nonperforming loans is a ratio to the value of all loans. Securitized loans/assets is computed only for banks that securitize. NFF denotes nonfinancial firms. Except for assets, variables are ratios in percentages. The second-last column shows the ratio of the test for the difference of the means, and the last column the normalized difference test of Imbens and Wooldridge (2009). See definitions in Appendix B. Source: Own computations on bank balance sheet data from the Bank of Spain. View Large Table 1. Descriptive statistics of healthy and weak banks (2006). Healthy banks Weak banks Mean St. dev. Mean St. dev. Mean t test Normalized difference ln(assets) 13.7 2.1 16.4 1.0 7.1 1.14 Own funds/assets 8.4 9.0 5.2 1.2 $$-$$2.0 $$-$$0.35 Liquidity/assets 23.7 22.4 11.5 4.5 $$-$$3.1 $$-$$0.54 Return on assets 1.0 1.7 0.9 0.3 $$-$$0.5 $$-$$0.09 Nonperforming loans 1.5 6.3 0.7 0.6 $$-$$0.7 $$-$$0.13 Nonperforming loans (2012) 8.6 12.7 22.0 6.0 3.5 0.95 Loans to REI/loans to NFF 36.8 22.3 67.9 8.1 7.9 1.31 Securitized loans/assets 14.9 10.5 18.5 6.3 1.6 0.30 Healthy banks Weak banks Mean St. dev. Mean St. dev. Mean t test Normalized difference ln(assets) 13.7 2.1 16.4 1.0 7.1 1.14 Own funds/assets 8.4 9.0 5.2 1.2 $$-$$2.0 $$-$$0.35 Liquidity/assets 23.7 22.4 11.5 4.5 $$-$$3.1 $$-$$0.54 Return on assets 1.0 1.7 0.9 0.3 $$-$$0.5 $$-$$0.09 Nonperforming loans 1.5 6.3 0.7 0.6 $$-$$0.7 $$-$$0.13 Nonperforming loans (2012) 8.6 12.7 22.0 6.0 3.5 0.95 Loans to REI/loans to NFF 36.8 22.3 67.9 8.1 7.9 1.31 Securitized loans/assets 14.9 10.5 18.5 6.3 1.6 0.30 Notes: There are 206 healthy and 33 weak banks. Nonperforming loans is a ratio to the value of all loans. Securitized loans/assets is computed only for banks that securitize. NFF denotes nonfinancial firms. Except for assets, variables are ratios in percentages. The second-last column shows the ratio of the test for the difference of the means, and the last column the normalized difference test of Imbens and Wooldridge (2009). See definitions in Appendix B. Source: Own computations on bank balance sheet data from the Bank of Spain. View Large The split between weak and healthy banks allows us to analyze the compound effect of these initial differences in lender health on credit supply, including latent losses not officially recognized until much later. The weak bank label should therefore be interpreted as a proxy for the relatively strong deterioration of the balance sheets and the lending capacity of the most vulnerable banks. 3.3. The Credit Collapse Figure 1 depicts the real value of the annual flow of new credit to nonfinancial firms by month and bank type (average over the past 12 months). It reveals that the flow of new credit grew significantly more at weak than at healthy banks during the boom—60% vs. 12% from 2002 to 2007—and it also fell more in the slump—46% vs. 35% from 2007 to 2010. This evolution stems from both the intensive and extensive margins. The latter is captured in Figure 2, which represents acceptance rates for loan applications by potential clients (nonclient firms). Initially, acceptance rates were higher for weak than for healthy banks, they then converged, subsequently both fell precipitously, and at the end of the period they were lower at weak banks. This evolution reflects the difficulties faced by Spanish firms trying to switch to a new lender during the crisis. Figure 1. View largeDownload slide New credit to nonfinancial firms by bank type (12-month backward moving average, 2007:10 = 100). Source: Banco de España. Figure 1. View largeDownload slide New credit to nonfinancial firms by bank type (12-month backward moving average, 2007:10 = 100). Source: Banco de España. Figure 2. View largeDownload slide Acceptance rates of loan applications by noncurrent clients, by bank type, 2002:4-2012:6 (%). Source: Banco de España. Figure 2. View largeDownload slide Acceptance rates of loan applications by noncurrent clients, by bank type, 2002:4-2012:6 (%). Source: Banco de España. Figure 3 shows that the average interest rates charged by the two sets of banks closely follow the ECB policy rate. Until the end of our sample period, the difference between them was always below 30 basis points. This suggests that interest rates were scarcely used by weak banks to ration credit demand during that period.8 We can therefore safely focus on the differential evolution of credit volume at the two sets of banks during the crisis. Figure 3. View largeDownload slide Average annual interest rate for new loans to nonfinancial firms by bank type and the policy rate, 2003:1-2012:6 (%). Source: Banco de España. Figure 3. View largeDownload slide Average annual interest rate for new loans to nonfinancial firms by bank type and the policy rate, 2003:1-2012:6 (%). Source: Banco de España. The same graphs also show that the consolidation operations and nationalizations during 2011–2012 did not restore the credit flow to weak banks. The gaps between bank types regarding new credit flows and acceptance rates continued to grow, and weak banks also started to ration credit by charging substantially higher average interest rates than healthy banks. 4. Data In this section, we describe our data set, the sample selection procedure, and the construction of the treatment and control groups. For further details see Appendix B. 4.1. Data Sources We construct a matched bank-firm data set with detailed information on all bank loans to nonfinancial firms. Even though our analysis focuses on the period 2006–2010, we collect data starting in 2000. The loan data are obtained from the Central Credit Register (CIR) of the Bank of Spain, which records all bank loans to nonfinancial firms above 6,000 euros (around 7,900 dollars at the end of 2006). Given the low threshold, these data can be taken as the census. The CIR provides the identity of the parties involved in a loan, the share of collateralized loans by firm, its maturity structure, the identity of its main bank—i.e., the one with the largest value of outstanding loans—, and indicators of its creditworthiness, such as the value of the firm's nonperforming and potentially problematic loans. It does neither record the interest rate nor the purpose of the loan. We therefore have to rely on the distinction between credit lines and loans to indirectly establish a shortage of working capital or of funds for investment.9 Apart from the information on new and outstanding loans, we also have access to loan applications from nonclients.10 By matching the records on loan applications with the CIR, we infer whether the loan materialized. If not, either the bank denied it or else the firm obtained funding elsewhere (Jiménez et al. 2012). Because the application data set only provides information on borrowing for firms with a credit history, we exclude firms with no prior loans. We gather economic and financial information for more than 300,000 private, nonfinancial firms from the mandatory annual balance sheets and income statements that Spanish corporations submit to the Mercantile Registers. Our source is the Iberian Balance Sheet Analysis System produced by INFORMA D&B in collaboration with Bureau Van Dijk and the Central Balance Sheet Data Office (CBSO) of the Bank of Spain. We match the data on loans, banks, and firms through firms’ tax ID. Employment is measured as the annual average of employees, where temporary workers are weighted according to their weeks of work. Iberian Balance Sheet Analysis System also provides information on variables such as the firm's age, size, and indebtedness, though for most firms we only observe an abridged balance sheet with no liability breakdown. Lastly, we observe the firm's industry and use a two-digit breakdown into 78 industries. To disentangle job losses in surviving firms from those due to firm closures, we use the Central Business Register (DIRCE), which allows us to ensure that firms that are in the sample in 2006 but which disappear from it in subsequent years have indeed closed down.11 Lastly, we exploit two databases on banks. The first one, used for supervisory purposes, records their financial statements. It includes 239 banks, comprising commercial banks, savings banks, and credit cooperatives. The second one contains historical data on the location of bank branches at the municipal level, which is used for the first time for research purposes. 4.2. The Treatment and Control Groups To analyze the employment effects of the credit reductions by weak banks, we divide the sample of firms into two groups depending on the strength of their precrisis relationship to weak banks. We measure weak-bank attachment through the ratio of the total amount of loans from weak banks to the firm's asset value. It is the product of the firm's ratio of debt with weak banks to total debt—i.e., the weight of weak banks in debt—and the ratio of total debt to asset value—leverage—and it is measured in 2006. Our baseline treatment measure is a dummy variable denoted WBi, which takes the value 1 if the weak-bank loan-to-asset ratio for firm i is above the first quartile of the distribution of firms with nonzero exposure. The chosen threshold for our weak-bank dummy has the advantage of excluding firms with marginal attachment to weak banks from the treatment group, while still providing a conservative estimate of the impact of such attachment, because the threshold is set at the lower end of the distribution.12 We will nevertheless show the robustness of our findings to the use of the continuous weak-bank loan-to-asset ratio measure and to different cutoff levels for the weak-bank dummy. Given the size of our data set, we adopt stringent sample selection rules. To avoid the problem of reverse causality—so that firms’ troubles drive banks’ problems rather than the opposite—we exclude firms in the REI or in two-digit industries selling at least 20% of their value added to the REI in 2000 (see Appendix B). This date is chosen to minimize potential endogeneity through credit decisions taken in the boom.13 Throughout the analysis we work with a balanced sample and we only include firms in our sample for which we have reliable observations on all variables from 2006 to 2010. In particular, we exclude firms that do not deposit their accounts after 2006 but still appear in the Central Business Register. Hence, only firms that are missing in both registers are classified as having closed down. Moreover, because we are interested in bank credit, we exclude firms with no loans in 2006. This leaves us with a final sample of 149,458 firms. We choose 2006 as the base year because both GDP and real credit were growing very quickly, at 4.1% and 19% p.a., respectively, so that neither the recession nor the credit crunch were generally anticipated then. However, in one specification we set 2007 as the base year to check the robustness of our results to this dating. In 2006, the firms in our sample represented 19% of firms, 28% of value added, and 42% of private sector employees in the industries included in our analysis. Most firms are very small, indeed, 98.7% of them are SMEs according to the European Commission definition (i.e., having less than 250 employees and either turnover below 50 million euros or a balance sheet total below 43 million euros). On average these firms reduced employment by 8.1% during the sample period. This figure is very close to the aggregate reduction in employment for the industries we cover. Table 2 presents descriptive statistics for our treatment and control groups. About 69% of firms have either no credit from weak banks or a weak-bank loan-to-asset ratio below the first quartile—which is equal to 4.8%. For firms above this threshold, the average share of credit from weak banks is equal to 68.5%, and their ratio of weak-bank credit to assets to 22.8%. Table 2. Descriptive statistics of control and treated firms (2006). Control Treated Mean St. dev. P25 P50 P75 Mean St. dev. P25 P50 P75 Mean t test Normalized difference Loans with WB/assets 0.3 0.9 0.0 0.0 0.0 22.8 17.1 9.7 17.3 30.9 427.3 1.31 Share of loans with WB 8.5 24.1 0.0 0.0 0.0 68.5 30.3 40.9 73.3 100.0 403.9 1.55 Employment (employees) 25.3 365.6 2.0 6.0 13.0 20.3 207.2 2.0 5.0 13.0 $$-$$2.7 $$-$$0.01 Temporary employment 20.4 25.4 0.0 11.1 33.3 22.7 26.0 0.0 14.5 36.6 16.0 $$-$$0.06 Age (years) 12.6 9.8 6.0 11.0 17.0 11.7 8.7 6.0 10.0 16.0 $$-$$17.1 $$-$$0.07 Size (million euros) 5.8 118.2 0.3 0.6 1.7 3.6 27.5 0.3 0.6 1.7 $$-$$4.0 $$-$$0.02 Exporter 13.0 33.7 0.0 0.0 0.0 13.1 33.7 0.0 0.0 0.0 0.3 0.00 Own funds/assets 34.4 23.8 14.2 30.3 51.1 24.9 18.5 10.0 20.8 35.8 $$-$$74.3 $$-$$0.31 Liquidity/assets 12.4 15.1 1.9 7.0 17.4 8.6 11.8 1.1 4.2 11.2 $$-$$47.3 $$-$$0.20 Return on assets 6.7 11.4 1.8 4.9 10.2 5.2 9.0 2.0 4.4 8.0 $$-$$23.8 $$-$$0.10 Bank debt 30.7 26.7 6.8 24.8 49.8 48.5 23.5 29.4 47.4 66.2 120.8 0.50 Short-term bank debt (≤1 year) 48.8 41.5 0.0 46.7 100.0 45.7 37.1 4.3 44.9 80.7 $$-$$13.2 $$-$$0.05 Long-term bank debt (≥5 years) 21.5 35.3 0.0 0.0 37.1 29.5 36.3 0.0 7.4 59.0 39.7 0.16 Noncollateralized bank debt 81.9 33.4 82.7 100.0 100.0 73.7 35.6 47.4 100.0 100.0 $$-$$42.3 $$-$$0.17 Credit line (has one) 69.0 46.3 0.0 100.0 100.0 72.2 44.8 0.0 100.0 100.0 12.5 0.05 Banking relationships (no.) 1.9 1.5 1.0 1.0 2.0 3.0 2.7 1.0 2.0 4.0 103.7 0.37 Current loan defaults 0.3 5.6 0.0 0.0 0.0 0.6 7.4 0.0 0.0 0.0 6.8 0.03 Past loan defaults 1.4 11.9 0.0 0.0 0.0 2.4 15.2 0.0 0.0 0.0 12.7 0.05 Past loan applications 54.2 49.8 0.0 100.00 100.00 68.9 46.3 0.0 100.0 100.0 52.7 0.22 All loan applications accepted 22.0 41.4 0.0 0.0 0.0 26.2 44.0 0.0 0.0 100.0 17.6 0.07 Control Treated Mean St. dev. P25 P50 P75 Mean St. dev. P25 P50 P75 Mean t test Normalized difference Loans with WB/assets 0.3 0.9 0.0 0.0 0.0 22.8 17.1 9.7 17.3 30.9 427.3 1.31 Share of loans with WB 8.5 24.1 0.0 0.0 0.0 68.5 30.3 40.9 73.3 100.0 403.9 1.55 Employment (employees) 25.3 365.6 2.0 6.0 13.0 20.3 207.2 2.0 5.0 13.0 $$-$$2.7 $$-$$0.01 Temporary employment 20.4 25.4 0.0 11.1 33.3 22.7 26.0 0.0 14.5 36.6 16.0 $$-$$0.06 Age (years) 12.6 9.8 6.0 11.0 17.0 11.7 8.7 6.0 10.0 16.0 $$-$$17.1 $$-$$0.07 Size (million euros) 5.8 118.2 0.3 0.6 1.7 3.6 27.5 0.3 0.6 1.7 $$-$$4.0 $$-$$0.02 Exporter 13.0 33.7 0.0 0.0 0.0 13.1 33.7 0.0 0.0 0.0 0.3 0.00 Own funds/assets 34.4 23.8 14.2 30.3 51.1 24.9 18.5 10.0 20.8 35.8 $$-$$74.3 $$-$$0.31 Liquidity/assets 12.4 15.1 1.9 7.0 17.4 8.6 11.8 1.1 4.2 11.2 $$-$$47.3 $$-$$0.20 Return on assets 6.7 11.4 1.8 4.9 10.2 5.2 9.0 2.0 4.4 8.0 $$-$$23.8 $$-$$0.10 Bank debt 30.7 26.7 6.8 24.8 49.8 48.5 23.5 29.4 47.4 66.2 120.8 0.50 Short-term bank debt (≤1 year) 48.8 41.5 0.0 46.7 100.0 45.7 37.1 4.3 44.9 80.7 $$-$$13.2 $$-$$0.05 Long-term bank debt (≥5 years) 21.5 35.3 0.0 0.0 37.1 29.5 36.3 0.0 7.4 59.0 39.7 0.16 Noncollateralized bank debt 81.9 33.4 82.7 100.0 100.0 73.7 35.6 47.4 100.0 100.0 $$-$$42.3 $$-$$0.17 Credit line (has one) 69.0 46.3 0.0 100.0 100.0 72.2 44.8 0.0 100.0 100.0 12.5 0.05 Banking relationships (no.) 1.9 1.5 1.0 1.0 2.0 3.0 2.7 1.0 2.0 4.0 103.7 0.37 Current loan defaults 0.3 5.6 0.0 0.0 0.0 0.6 7.4 0.0 0.0 0.0 6.8 0.03 Past loan defaults 1.4 11.9 0.0 0.0 0.0 2.4 15.2 0.0 0.0 0.0 12.7 0.05 Past loan applications 54.2 49.8 0.0 100.00 100.00 68.9 46.3 0.0 100.0 100.0 52.7 0.22 All loan applications accepted 22.0 41.4 0.0 0.0 0.0 26.2 44.0 0.0 0.0 100.0 17.6 0.07 Notes: Observations—149,458 firms; 106,128 control; and 43,330 treated firms. WB denotes weak banks. Variables are ratios in percentages unless otherwise indicated. The twelfth column shows the t-ratio on the test for the difference of the means and the last column the normalized difference test of Imbens and Wooldridge (2009). See definitions in Appendix B. View Large Table 2. Descriptive statistics of control and treated firms (2006). Control Treated Mean St. dev. P25 P50 P75 Mean St. dev. P25 P50 P75 Mean t test Normalized difference Loans with WB/assets 0.3 0.9 0.0 0.0 0.0 22.8 17.1 9.7 17.3 30.9 427.3 1.31 Share of loans with WB 8.5 24.1 0.0 0.0 0.0 68.5 30.3 40.9 73.3 100.0 403.9 1.55 Employment (employees) 25.3 365.6 2.0 6.0 13.0 20.3 207.2 2.0 5.0 13.0 $$-$$2.7 $$-$$0.01 Temporary employment 20.4 25.4 0.0 11.1 33.3 22.7 26.0 0.0 14.5 36.6 16.0 $$-$$0.06 Age (years) 12.6 9.8 6.0 11.0 17.0 11.7 8.7 6.0 10.0 16.0 $$-$$17.1 $$-$$0.07 Size (million euros) 5.8 118.2 0.3 0.6 1.7 3.6 27.5 0.3 0.6 1.7 $$-$$4.0 $$-$$0.02 Exporter 13.0 33.7 0.0 0.0 0.0 13.1 33.7 0.0 0.0 0.0 0.3 0.00 Own funds/assets 34.4 23.8 14.2 30.3 51.1 24.9 18.5 10.0 20.8 35.8 $$-$$74.3 $$-$$0.31 Liquidity/assets 12.4 15.1 1.9 7.0 17.4 8.6 11.8 1.1 4.2 11.2 $$-$$47.3 $$-$$0.20 Return on assets 6.7 11.4 1.8 4.9 10.2 5.2 9.0 2.0 4.4 8.0 $$-$$23.8 $$-$$0.10 Bank debt 30.7 26.7 6.8 24.8 49.8 48.5 23.5 29.4 47.4 66.2 120.8 0.50 Short-term bank debt (≤1 year) 48.8 41.5 0.0 46.7 100.0 45.7 37.1 4.3 44.9 80.7 $$-$$13.2 $$-$$0.05 Long-term bank debt (≥5 years) 21.5 35.3 0.0 0.0 37.1 29.5 36.3 0.0 7.4 59.0 39.7 0.16 Noncollateralized bank debt 81.9 33.4 82.7 100.0 100.0 73.7 35.6 47.4 100.0 100.0 $$-$$42.3 $$-$$0.17 Credit line (has one) 69.0 46.3 0.0 100.0 100.0 72.2 44.8 0.0 100.0 100.0 12.5 0.05 Banking relationships (no.) 1.9 1.5 1.0 1.0 2.0 3.0 2.7 1.0 2.0 4.0 103.7 0.37 Current loan defaults 0.3 5.6 0.0 0.0 0.0 0.6 7.4 0.0 0.0 0.0 6.8 0.03 Past loan defaults 1.4 11.9 0.0 0.0 0.0 2.4 15.2 0.0 0.0 0.0 12.7 0.05 Past loan applications 54.2 49.8 0.0 100.00 100.00 68.9 46.3 0.0 100.0 100.0 52.7 0.22 All loan applications accepted 22.0 41.4 0.0 0.0 0.0 26.2 44.0 0.0 0.0 100.0 17.6 0.07 Control Treated Mean St. dev. P25 P50 P75 Mean St. dev. P25 P50 P75 Mean t test Normalized difference Loans with WB/assets 0.3 0.9 0.0 0.0 0.0 22.8 17.1 9.7 17.3 30.9 427.3 1.31 Share of loans with WB 8.5 24.1 0.0 0.0 0.0 68.5 30.3 40.9 73.3 100.0 403.9 1.55 Employment (employees) 25.3 365.6 2.0 6.0 13.0 20.3 207.2 2.0 5.0 13.0 $$-$$2.7 $$-$$0.01 Temporary employment 20.4 25.4 0.0 11.1 33.3 22.7 26.0 0.0 14.5 36.6 16.0 $$-$$0.06 Age (years) 12.6 9.8 6.0 11.0 17.0 11.7 8.7 6.0 10.0 16.0 $$-$$17.1 $$-$$0.07 Size (million euros) 5.8 118.2 0.3 0.6 1.7 3.6 27.5 0.3 0.6 1.7 $$-$$4.0 $$-$$0.02 Exporter 13.0 33.7 0.0 0.0 0.0 13.1 33.7 0.0 0.0 0.0 0.3 0.00 Own funds/assets 34.4 23.8 14.2 30.3 51.1 24.9 18.5 10.0 20.8 35.8 $$-$$74.3 $$-$$0.31 Liquidity/assets 12.4 15.1 1.9 7.0 17.4 8.6 11.8 1.1 4.2 11.2 $$-$$47.3 $$-$$0.20 Return on assets 6.7 11.4 1.8 4.9 10.2 5.2 9.0 2.0 4.4 8.0 $$-$$23.8 $$-$$0.10 Bank debt 30.7 26.7 6.8 24.8 49.8 48.5 23.5 29.4 47.4 66.2 120.8 0.50 Short-term bank debt (≤1 year) 48.8 41.5 0.0 46.7 100.0 45.7 37.1 4.3 44.9 80.7 $$-$$13.2 $$-$$0.05 Long-term bank debt (≥5 years) 21.5 35.3 0.0 0.0 37.1 29.5 36.3 0.0 7.4 59.0 39.7 0.16 Noncollateralized bank debt 81.9 33.4 82.7 100.0 100.0 73.7 35.6 47.4 100.0 100.0 $$-$$42.3 $$-$$0.17 Credit line (has one) 69.0 46.3 0.0 100.0 100.0 72.2 44.8 0.0 100.0 100.0 12.5 0.05 Banking relationships (no.) 1.9 1.5 1.0 1.0 2.0 3.0 2.7 1.0 2.0 4.0 103.7 0.37 Current loan defaults 0.3 5.6 0.0 0.0 0.0 0.6 7.4 0.0 0.0 0.0 6.8 0.03 Past loan defaults 1.4 11.9 0.0 0.0 0.0 2.4 15.2 0.0 0.0 0.0 12.7 0.05 Past loan applications 54.2 49.8 0.0 100.00 100.00 68.9 46.3 0.0 100.0 100.0 52.7 0.22 All loan applications accepted 22.0 41.4 0.0 0.0 0.0 26.2 44.0 0.0 0.0 100.0 17.6 0.07 Notes: Observations—149,458 firms; 106,128 control; and 43,330 treated firms. WB denotes weak banks. Variables are ratios in percentages unless otherwise indicated. The twelfth column shows the t-ratio on the test for the difference of the means and the last column the normalized difference test of Imbens and Wooldridge (2009). See definitions in Appendix B. View Large Compared with the control group, firms in the treatment group seem to be on average younger and smaller, they have more temporary workers, and they are as likely to be exporters. The data also reflect the worse financial profile of firms in the treatment group: They are less profitable, hold less capital and liquid assets, and they are more indebted to banks, although the average maturity of their loans is higher. In addition, they work with more banks and over 2002–2006 they defaulted more often on their loans. They also applied for loans more often and had a higher acceptance rate. These differences are significant according to the t-ratio, but in very large samples this statistic has the problem that it increases with the number of observations. Imbens and Wooldridge (2009) propose a scale-free alternative measure, the difference in averages scaled by the square root of the sum of the variances. Indeed, as shown in the last two columns of Table 2, the results from these two tests diverge in our case. Using the normalized difference test and the heuristic threshold of 0.25 suggested by Imbens and Rubin (2015), the only significant difference is that firms exposed to weak banks have a lower degree of capitalization and a higher level of indebtedness, and they work with more banks than nonexposed firms. Their lower liquidity and higher number of past loan applications are close to being significant. This implies, first of all, that selection on observables is not a very important problem, once we take into account the large sample used. Second, this also means that we should control for those three firm-level characteristics—or at most five—in our empirical analysis. Nevertheless, we will use all 17 variables listed in the table below the employment level as controls in our firm-level credit and employment estimation to be sure that we are conditionally comparing very similar firms. At this stage, we need to deal with the potential objection that our treatment is defined in terms of an outcome, a bank's bailout, that is realized after the crisis broke out. Using an ex-post criterion does not invalidate our results, however, as long as the outcome was unexpected. To study whether firms could have anticipated in 2006 the future solvency problems of weak banks, we analyze the risk premia charged to Spanish banks’ securitization issues prior to the recession. We use data on tranches of mortgage backed securities and asset backed securities in 2006, grouping the ratings into prime (AAA), investment grade (AA+ to BBB−), and speculative (BB+ to D). We have 303 observations (deal-tranches) from Dealogic, with floating rate, quarterly coupon frequency, and referenced to the 3-month Euribor, from 24 issuer parents. Without any controls, weak banks actually paid seven basis points less than healthy banks. To control for issue characteristics, we regress coupon differentials in basis points on a set of variables capturing the type of securitization, risk category, month of issue, years to maturity, collateral type, and guarantor type. Standard errors are clustered by issuer parent. The estimated coefficient associated with the weak-bank dummy is positive but nonsignificant: 2.8 basis points, with a p-value of 0.55 (see Table A.2). Hence, we cannot reject the hypothesis that financial markets failed to recognize the buildup of differential risk at weak banks in 2006.14 It seems safe to assume that private firms, with a lower capacity to process available information than financial markets, could not possibly have predicted it either. 5. Empirical Strategy Our identification strategy proceeds in two steps. The first step consists of establishing the presence of a credit supply shock associated with the troubles of weak banks. In this part, we first estimate a credit equation at the bank-firm level and then at the firm level. The second part consists of estimating the effects of weak-bank attachment on employment. 5.1. Identification of the Credit Supply Shock We start by estimating the following credit growth equation for bank-firm pairs:15 \begin{equation} \Delta _{\tau }\log (1+ {\mathit{Credit}}_{ib})=\theta _{i}+\pi WB_{b}+Z_{ib}^{\prime }\kappa +S_{b}^{\prime }\lambda +\epsilon _{ib}, \end{equation} (1) where Δτ is a τ-year difference with respect to the year 2006, $$ {\mathit{Credit}}_{ib}$$ is total credit committed by bank b to firm i—both drawn and undrawn, so as to minimize potential endogeneity—, θi is a firm fixed effect, WBb is a dummy variable that takes the value 1 if bank b is weak, Zib is a vector of bank-firm controls that includes the length of their relationship and a dummy variable for past defaults, Sb is a vector of bank controls, and εib is a random shock. Our coefficient of interest is π. Specifications like (1) are the standard procedure to identify credit supply shocks. The fixed effects absorb any differences in observable and unobservable firm characteristics. As a result, they perfectly control for potentially confounding demand effects, allowing us to test whether the same firm experiences a larger reduction in lending from weak banks than from healthy banks once we control for differences in Zib and Sb. This equation can however be estimated only for firms that work with more than one bank. Because many firms in our sample work with a single bank, we also estimate a between-firm variant of equation (1) in which the firm fixed effects are replaced by a vector Xi of firm controls. As originally explained by Khwaja and Mian (2008), this ordinary least squares (OLS) specification may yield biased estimates of π in the presence of both credit demand and supply shocks, but we show that this risk can be minimized by introducing a rich set of firm controls and industry times municipality dummies to control for demand effects. Next, even if we confirm the presence of a credit shock at the bank-firm level, we still need to check whether the affected firms managed to offset the reduction in credit supply by weak banks with additional loans from other banks. For this purpose, we estimate the following firm-level equation: \begin{equation} \Delta _{\tau }\log ( 1+ {\mathit{Credit}}_{ij}) =\rho +\mu WB_{i}+X_{i}^{\prime }\eta +\delta _{j}+v_{ij}, \end{equation} (2) which links credit growth to our treatment variable WBi, where Xi contains the 17 variables listed in Table 2, and δj is a vector of industry (78) times municipality (2,749) dummies that control for local credit demand conditions. Here, our coefficient of interest is μ, which will typically be smaller than π to the extent that firms managed to obtain credit from healthy banks when weak banks curtailed their supply. 5.2. The Employment Impact of Credit Constraints We then proceed to estimate the impact of the credit supply shock on employment. To ensure that our estimates do not capture the effect of differences in observable characteristics of firms rather than the effect of credit supply, we adopt a DD specification in growth rates that has the same structure as equation (2) (Wooldridge 2010): \begin{equation} \Delta _{\tau }\log ( 1+n_{ij}) =\alpha +\beta WB_{i}+X_{i}^{\prime }\gamma +\delta _{j}+u_{ij,} \end{equation} (3) where nij is employment in firm i in industry-municipality cell j and uij is a random shock. All regressors are again measured in 2006. This estimate is an average treatment effect on the treated. To measure the employment adjustment in both surviving and closing firms, we set nij to zero for firms that are present in 2006 but have closed down τ years later. Estimating in differences implies that we are including an aggregate trend and differential trends by industry-municipality cells and by firm characteristics, which is substantially more demanding than the standard DD specification in levels. Unbiased estimation of the causal impact of weak-bank attachment on employment however relies on the unconfoundedness assumption, which requires the assignment of firms to the treatment and control groups to be completely random conditional on the controls for observables. Moreover, unlike for credit, this specification cannot perfectly control for confounding factors through the introduction of fixed effects. The main threat to identification is the nonrandom assignment of firms to banks before the crisis. Aggregate shocks may differentially affect firms depending on their profitability, product quality, or financial vulnerability. If, for example, the crisis hit more financially vulnerable firms harder and these firms were over-represented among the clients of weak banks, then the DD specification would tend to overestimate the real effects of the credit shock. Our firm controls, Xi, are meant to absorb potential differences in both firms’ performance and their financial vulnerability and creditworthiness, but selection may take place on both observables and unobservables. This may not be an overriding problem, because only 3 of the 17 firm characteristics that we use are statistically different, but we still devote Section 8 to deal with this issue. The other main concern is that demand effects may bias our estimation (Mian and Sufi 2014). Before the crisis, lending grew especially in the real estate industry and it was more concentrated in certain areas, where in the recession we might observe both a larger drop in demand by households and a higher density of (non-REI) firms exposed to weak banks. In these circumstances, employment reductions would stem from lower consumption demand rather than from less credit. The fact that small firms tend to be financed by local banks (Petersen and Rajan 2002; Guiso, Pistaferri, and Schivardi 2013) would additionally contribute to the presence of local demand effects. For this reason, we allow for differential trends in the δj cells defined by the product of two-digit industry and municipality dummy variables. 6. The Differential Evolution of Credit The first step is to validate our claim that the differential evolution of the volume of lending by the two sets of banks reflects a credit supply shock, which we carry out through both bank-firm and firm-level analyses. 6.1. Bank-Firm Analysis Table 3 reports the results for our baseline equation (1) and alternative specifications for the change in credit between 2006 and 2010. Robust standard errors are corrected for multiclustering at the firm and bank level. The specification with firm controls and industry-municipality dummies yields an estimated differential reduction in credit of 23.2 pp for weak banks vis-à-vis healthy banks (column 1). Restricting the sample to firms with multiple banking relationships reduces the estimate to −25.6 pp (column 2), which is virtually identical to the estimate for our baseline specification with firm fixed effects, −25.5 pp, estimated with the same sample of multibank firms (column 3). The similarity between these two estimates suggests that unobservables do not play a significant role in access to credit, despite the differences in three of the observable firm characteristics. Moreover, a Hausman test fails to reject the null hypothesis of orthogonality between the firm fixed effects and WBb with a p-value of 0.372. These results confirm that our weak-bank dummy variable captures changes in credit supply rather than in credit demand. Table 3. Credit rationing at the firm-bank level. Dependent variable: $${\Delta }_{4}\log {(1+ {\mathit Credit}}_{ijb})$$. (1) (2) (3) (4) (5) (6) All firms Multibank Fixed effects Interactions Positive credit Real estate $${\mathit {WB}}_{b}$$ $$-$$0.232$$^{^{{ \ast \ast \ast }}}$$ $$-$$0.256$$^{^{{ \ast \ast \ast } }}$$ $$-$$0.255$$^{^{{ \ast \ast \ast }}}$$ $$-$$0.079$$^{^{{ \ast \ast }}}$$ $$-$$0.180$$^{^{{ \ast }}}$$ (0.088) (0.094) (0.008) (0.034) (0.096) $${ I}$$(Credit lineib) 0.074$$^{^{{ \ast \ast \ast }}}$$ (0.015) $${ I}$$(Credit lineib) $$\times {\mathit {WB}} _{{b}}$$ $$-$$0.106$$^{^{{ \ast \ast }}}$$ (0.039) Firm fixed effects No No Yes Yes Yes Yes Firm controls Yes Yes – – – – Bank fixed effects No No No Yes No No Bank controls Yes Yes Yes Yes Yes Yes Firm-bank controls Yes Yes Yes Yes Yes Yes Industry × province fixed effects Yes Yes – – – – Several banks No Yes Yes Yes Yes Yes Balance-sheet data Yes Yes Yes Yes Yes Yes $${ R}^{{2}}$$ 0.060 0.059 0.407 0.452 0.394 0.406 No. obs. 304,089 236,691 236,691 236,691 126,863 236,691 No. firms 139,685 72,287 72,287 72,287 42,630 72,287 (1) (2) (3) (4) (5) (6) All firms Multibank Fixed effects Interactions Positive credit Real estate $${\mathit {WB}}_{b}$$ $$-$$0.232$$^{^{{ \ast \ast \ast }}}$$ $$-$$0.256$$^{^{{ \ast \ast \ast } }}$$ $$-$$0.255$$^{^{{ \ast \ast \ast }}}$$ $$-$$0.079$$^{^{{ \ast \ast }}}$$ $$-$$0.180$$^{^{{ \ast }}}$$ (0.088) (0.094) (0.008) (0.034) (0.096) $${ I}$$(Credit lineib) 0.074$$^{^{{ \ast \ast \ast }}}$$ (0.015) $${ I}$$(Credit lineib) $$\times {\mathit {WB}} _{{b}}$$ $$-$$0.106$$^{^{{ \ast \ast }}}$$ (0.039) Firm fixed effects No No Yes Yes Yes Yes Firm controls Yes Yes – – – – Bank fixed effects No No No Yes No No Bank controls Yes Yes Yes Yes Yes Yes Firm-bank controls Yes Yes Yes Yes Yes Yes Industry × province fixed effects Yes Yes – – – – Several banks No Yes Yes Yes Yes Yes Balance-sheet data Yes Yes Yes Yes Yes Yes $${ R}^{{2}}$$ 0.060 0.059 0.407 0.452 0.394 0.406 No. obs. 304,089 236,691 236,691 236,691 126,863 236,691 No. firms 139,685 72,287 72,287 72,287 42,630 72,287 Notes: OLS estimates for 2010. Bank controls: log of total assets, leverage ratio, liquidity ratio, rate of return on assets and provisions normalized by net interest income. Firm-bank controls: length of firm-bank relationship in months and past defaults. Firm control variables: see Table 2. “Yes/no/–” indicates whether the corresponding set of variables is either included, not included or redundant. Robust standard errors corrected for multiclustering at the firm and bank level appear between parentheses. Significance levels: *$${p} <$$ 0.10, **$${p} < $$ 0.05, ***$${p} < $$ 0.01. View Large Table 3. Credit rationing at the firm-bank level. Dependent variable: $${\Delta }_{4}\log {(1+ {\mathit Credit}}_{ijb})$$. (1) (2) (3) (4) (5) (6) All firms Multibank Fixed effects Interactions Positive credit Real estate $${\mathit {WB}}_{b}$$ $$-$$0.232$$^{^{{ \ast \ast \ast }}}$$ $$-$$0.256$$^{^{{ \ast \ast \ast } }}$$ $$-$$0.255$$^{^{{ \ast \ast \ast }}}$$ $$-$$0.079$$^{^{{ \ast \ast }}}$$ $$-$$0.180$$^{^{{ \ast }}}$$ (0.088) (0.094) (0.008) (0.034) (0.096) $${ I}$$(Credit lineib) 0.074$$^{^{{ \ast \ast \ast }}}$$ (0.015) $${ I}$$(Credit lineib) $$\times {\mathit {WB}} _{{b}}$$ $$-$$0.106$$^{^{{ \ast \ast }}}$$ (0.039) Firm fixed effects No No Yes Yes Yes Yes Firm controls Yes Yes – – – – Bank fixed effects No No No Yes No No Bank controls Yes Yes Yes Yes Yes Yes Firm-bank controls Yes Yes Yes Yes Yes Yes Industry × province fixed effects Yes Yes – – – – Several banks No Yes Yes Yes Yes Yes Balance-sheet data Yes Yes Yes Yes Yes Yes $${ R}^{{2}}$$ 0.060 0.059 0.407 0.452 0.394 0.406 No. obs. 304,089 236,691 236,691 236,691 126,863 236,691 No. firms 139,685 72,287 72,287 72,287 42,630 72,287 (1) (2) (3) (4) (5) (6) All firms Multibank Fixed effects Interactions Positive credit Real estate $${\mathit {WB}}_{b}$$ $$-$$0.232$$^{^{{ \ast \ast \ast }}}$$ $$-$$0.256$$^{^{{ \ast \ast \ast } }}$$ $$-$$0.255$$^{^{{ \ast \ast \ast }}}$$ $$-$$0.079$$^{^{{ \ast \ast }}}$$ $$-$$0.180$$^{^{{ \ast }}}$$ (0.088) (0.094) (0.008) (0.034) (0.096) $${ I}$$(Credit lineib) 0.074$$^{^{{ \ast \ast \ast }}}$$ (0.015) $${ I}$$(Credit lineib) $$\times {\mathit {WB}} _{{b}}$$ $$-$$0.106$$^{^{{ \ast \ast }}}$$ (0.039) Firm fixed effects No No Yes Yes Yes Yes Firm controls Yes Yes – – – – Bank fixed effects No No No Yes No No Bank controls Yes Yes Yes Yes Yes Yes Firm-bank controls Yes Yes Yes Yes Yes Yes Industry × province fixed effects Yes Yes – – – – Several banks No Yes Yes Yes Yes Yes Balance-sheet data Yes Yes Yes Yes Yes Yes $${ R}^{{2}}$$ 0.060 0.059 0.407 0.452 0.394 0.406 No. obs. 304,089 236,691 236,691 236,691 126,863 236,691 No. firms 139,685 72,287 72,287 72,287 42,630 72,287 Notes: OLS estimates for 2010. Bank controls: log of total assets, leverage ratio, liquidity ratio, rate of return on assets and provisions normalized by net interest income. Firm-bank controls: length of firm-bank relationship in months and past defaults. Firm control variables: see Table 2. “Yes/no/–” indicates whether the corresponding set of variables is either included, not included or redundant. Robust standard errors corrected for multiclustering at the firm and bank level appear between parentheses. Significance levels: *$${p} <$$ 0.10, **$${p} < $$ 0.05, ***$${p} < $$ 0.01. View Large Was credit rationing by weak banks stronger on short-term funding? To answer this question, we interact WBb with an indicator for firms that enjoyed a credit line in 2006. The results in Table 3 indicate that weak banks reduced credit to firms with credit lines by 10.6 pp more than healthy banks (column 4). A natural interpretation is that credit lines were the easiest loans to cut for banks in distress and, possibly, that the credit constraint affected more working capital than investment. In Appendix Table A.3, we present the results when we also include dummies for maturities of 1–3 years, 3–5 years, above 5 years, and for unknown maturity (affecting 4% of the loans), with loans below 1 year being the reference category, and their interactions with the weak-bank dummy variable. The estimates do not indicate a differential effect of the credit supply shock for different loan maturities, as none of the coefficients of the interactions is statistically significant. Next, we show the estimate for bank-firm relationships that were still alive in 2010 (column 5). In this case, the difference in the reduction of credit supply is equal to 7.9 pp, indicating that adjustments at the internal margin—i.e., reductions in loan volume to existing lenders—account for a small share of the reduction in lending by weak banks, so that the external margin dominates—i.e., committed credit is reduced to zero or renewal of expired loans is denied. The differential effect captured by the weak-bank dummy indicates that standard measures of bank health do not fully capture the deterioration of weak banks’ assets. A natural explanation for this finding relies on differences in banks’ precrisis exposure to the REI. We measure it by the 2006 share of each bank's loans to firms in the REI and create a dummy variable that takes the value 1 for banks in the upper quartile of the cross-sectional distribution. The associated coefficient is 7.5 pp smaller and less significant than in our baseline (column 6). Hence, latent losses elsewhere in the balance sheets of weak banks may have been imperfectly correlated with their exposure to the REI. Lastly, our identification procedure relies on the absence of different precrisis trends in access to credit for firms in the treatment and control groups, which would lead to biased estimates. To check this issue, Panel (a) of Figure 4 shows the yearly coefficients, from 2004 to 2010, for our baseline specification with firm fixed effects. The coefficient of WBb is not significantly different from zero between 2004 and 2007; indeed, except for 2004, the point estimates are equal to zero. The treatment effect becomes significant in 2008 and it grows over time from −10 pp in 2008 to −25 pp in 2010. This shows that weak-bank exposure has no significant impact on access to credit prior to 2007 once we control for firm fixed effects.16 In sum, we have shown that weak banks reduced credit more than healthy banks, not just in the aggregate but also at the level of individual bank-firm relationships. Figure 4. View largeDownload slide Effect of weak-bank attachment on credit. Source: Authors’ computations using the data set. (a) Effect at the bank-firm level, 2004–2010 (pp). (b) Effect at the firm level, 2002–2010 (pp). Figure 4. View largeDownload slide Effect of weak-bank attachment on credit. Source: Authors’ computations using the data set. (a) Effect at the bank-firm level, 2004–2010 (pp). (b) Effect at the firm level, 2002–2010 (pp). 6.2. Firm-Level Analysis We now study credit rationing at the firm level. The dependent variable is the log difference between the firm's total credit outstanding in 2006 and 2010, and the weak-bank indicator of the bank-firm analysis is replaced by our treatment dummy WBi. The estimated drop in credit supply at the firm level of 5.3 pp in column (1) of Table 4 indicates that treated firms managed to offset around two-thirds of the fall in credit supply by weak banks. The corresponding estimate for multibank firms is −3.1 pp (column 2). Using the weak-bank measure based on REI exposure yields a smaller effect on credit, although it is not statistically different from the baseline estimate (column 3).17 Furthermore, although multibank firms suffered a stronger credit supply contraction at the local level than the average client firm of weak banks, the reverse is true at the firm level. A precrisis banking relationship with more than one bank thus provided some insurance against the shocks that subsequently hit weak banks. The average change in credit is equal to −23.1% for unattached firms and to −31.3% for attached firms. Out of this 8.2 pp difference, 2.8 pp are due to the attachment to weak banks, which therefore explains 34% of the fall in credit for attached firms. Table 4. Credit rationing at the firm level. Dependent variable: $${ \Delta }_{4}\log { (1+ \mathit{Credit}}_{ij}{ )}$$. (1) (2) (3) All firms Multibank Real estate $$\mathit{WB}_{i}$$ $$-$$0.053$$^{^{{ \ast \ast \ast }}}$$ $$-$$0.031$$^{^{{ \ast \ast \ast } }}$$ $$-$$0.039$$^{^{{ \ast \ast \ast }}}$$ (0.015) (0.011) (0.017) Firm controls Yes Yes Yes Industry × municipality fixed effects Yes Yes Yes Multiple banking relationships No Yes No Balance-sheet data Yes Yes Yes $${ R}^{2}$$ 0.215 0.246 0.215 No. obs. 149,458 74,045 149,458 (1) (2) (3) All firms Multibank Real estate $$\mathit{WB}_{i}$$ $$-$$0.053$$^{^{{ \ast \ast \ast }}}$$ $$-$$0.031$$^{^{{ \ast \ast \ast } }}$$ $$-$$0.039$$^{^{{ \ast \ast \ast }}}$$ (0.015) (0.011) (0.017) Firm controls Yes Yes Yes Industry × municipality fixed effects Yes Yes Yes Multiple banking relationships No Yes No Balance-sheet data Yes Yes Yes $${ R}^{2}$$ 0.215 0.246 0.215 No. obs. 149,458 74,045 149,458 Notes: OLS estimates for 2010. Control variables: see Table 2. Robust standard errors corrected for multiclustering at the industry, municipality, and main bank levels appear between parentheses. Significance level: ***p < 0.01. View Large Table 4. Credit rationing at the firm level. Dependent variable: $${ \Delta }_{4}\log { (1+ \mathit{Credit}}_{ij}{ )}$$. (1) (2) (3) All firms Multibank Real estate $$\mathit{WB}_{i}$$ $$-$$0.053$$^{^{{ \ast \ast \ast }}}$$ $$-$$0.031$$^{^{{ \ast \ast \ast } }}$$ $$-$$0.039$$^{^{{ \ast \ast \ast }}}$$ (0.015) (0.011) (0.017) Firm controls Yes Yes Yes Industry × municipality fixed effects Yes Yes Yes Multiple banking relationships No Yes No Balance-sheet data Yes Yes Yes $${ R}^{2}$$ 0.215 0.246 0.215 No. obs. 149,458 74,045 149,458 (1) (2) (3) All firms Multibank Real estate $$\mathit{WB}_{i}$$ $$-$$0.053$$^{^{{ \ast \ast \ast }}}$$ $$-$$0.031$$^{^{{ \ast \ast \ast } }}$$ $$-$$0.039$$^{^{{ \ast \ast \ast }}}$$ (0.015) (0.011) (0.017) Firm controls Yes Yes Yes Industry × municipality fixed effects Yes Yes Yes Multiple banking relationships No Yes No Balance-sheet data Yes Yes Yes $${ R}^{2}$$ 0.215 0.246 0.215 No. obs. 149,458 74,045 149,458 Notes: OLS estimates for 2010. Control variables: see Table 2. Robust standard errors corrected for multiclustering at the industry, municipality, and main bank levels appear between parentheses. Significance level: ***p < 0.01. View Large The large difference between the bank-firm and firm-level estimates may seem surprising, but weak banks may have predominantly severed their relationship with those firms with a marginal attachment to weak banks that are included in the control group. This would be consistent with our estimates for the firm-level effects being close to the estimated effects at the bank-firm level for continuing relationships (Table 3, column 5). It is also worth noting that our results are at variance with those in Jiménez et al. (2014), who—using the same CIR data—find a positive credit shock for banks that securitized mortgages in the years of the Spanish boom (2004Q4 to 2007Q4), but then find no transmission of this positive shock at the firm level. At that time, the credit market was booming and acceptance rates for loan applications were high for all banks, as shown in Section 3.3. On the contrary, the steep fall in acceptance rates during our sample period made it much harder for firms to offset credit rationing by weak banks through new loans from healthy banks. Our results are qualitatively similar to those in Cingano et al. (2016), who use data on Italian firms to estimate the real effects of the bank lending channel exploiting the 2007 liquidity drought in interbank markets as a source of variation in banks’ credit supply. The comparison is not straightforward, because they define treatment based on the ratio between a bank's interbank market loans and its asset value. Contrary to Jiménez et al. (2014) and to our case, they find similar coefficient estimates at the bank-firm and firm levels. Their estimate implies that a 1 pp increase in the interbank-to-asset ratio leads to a reduction in credit growth of 2.4 pp for a firm with a degree of exposure that is 1 standard deviation above the mean. Gobbi and Sette (2014) also study credit growth at the firm level for Italian firms during the Great Recession, finding that the number of banking relationships has a negative impact on credit growth, with the effect being strongest when firms move from one to two banks. In contrast, in the bank-firm analysis we find that the negative effect of weak-bank attachment is larger for multibank firms than for single-bank firms, whereas in the firm-level analysis the opposite holds. The latter is the most relevant evidence regarding the effect of the credit crunch, and when estimated for all firms (Table 4, column 1) the coefficient on a control variable for the number of banking relationships is equal to 0.022 (s.e. 0.006), which means that single-bank firms fared worse in terms of getting credit, and more so if attached to weak banks.18 7. Main Results This section presents the empirical results for our baseline specification for the employment effects of credit constraints and for a set of robustness checks. 7.1. Difference in Differences Table 5 presents the estimation results for our baseline DD equation (3). We report robust standard errors corrected for multiclustering at industry, municipality, and main bank level. In order to illustrate the sensitivity of our estimates to changes in the set of control variables, we subsequently add more controls until we arrive at our baseline specification. Table 5. The employment effect of weak-bank attachment. Difference in differences. Dependent variable: Δ4log (1 + nij). (1) (2) (3) (4) (5) (6) Sign. ctrls Baseline Placebo $$\mathit{WB}_{i}$$ $$-$$0.074$$^{^{{ \ast \ast \ast }}}$$ $$-$$0.076$$^{^{{ \ast \ast \ast } }}$$ $$-$$0.035$$^{^{{ \ast \ast \ast }}}$$ $$-$$0.028$$^{^{{ \ast \ast \ast }}}$$ $$-$$0.028$$^{^{{ \ast \ast }}}$$ 0.006 (0.013) (0.010) (0.006) (0.006) (0.007) (0.007) Firm controls (1) No No Yes Yes Yes Yes Firm controls (2) No No No Yes Yes Yes Municipality fixed effects Yes – – – – – Industry fixed effects Yes – – – – – Industry × municipality fixed effects No Yes Yes Yes Yes Yes Main bank fixed effects No No No No Yes No $${ R}^{2}$$ 0.046 0.150 0.155 0.177 0.179 0.203 No. obs. 149,458 149,458 149,458 149,458 149,458 112,933 (1) (2) (3) (4) (5) (6) Sign. ctrls Baseline Placebo $$\mathit{WB}_{i}$$ $$-$$0.074$$^{^{{ \ast \ast \ast }}}$$ $$-$$0.076$$^{^{{ \ast \ast \ast } }}$$ $$-$$0.035$$^{^{{ \ast \ast \ast }}}$$ $$-$$0.028$$^{^{{ \ast \ast \ast }}}$$ $$-$$0.028$$^{^{{ \ast \ast }}}$$ 0.006 (0.013) (0.010) (0.006) (0.006) (0.007) (0.007) Firm controls (1) No No Yes Yes Yes Yes Firm controls (2) No No No Yes Yes Yes Municipality fixed effects Yes – – – – – Industry fixed effects Yes – – – – – Industry × municipality fixed effects No Yes Yes Yes Yes Yes Main bank fixed effects No No No No Yes No $${ R}^{2}$$ 0.046 0.150 0.155 0.177 0.179 0.203 No. obs. 149,458 149,458 149,458 149,458 149,458 112,933 Notes: OLS estimates for 2010, except for column (6), which is dated in 2006. Control variables: see Table 2. “Yes/no/–” indicates whether the corresponding set of variables is either included, not included, or redundant. In column (3) only performance-related firm control variables are included. Robust standard errors corrected for multiclustering at the industry, municipality, and main bank levels appear between parentheses. Significance levels: **$${p} < $$ 0.05, ***$${p} <$$ 0.01. View Large Table 5. The employment effect of weak-bank attachment. Difference in differences. Dependent variable: Δ4log (1 + nij). (1) (2) (3) (4) (5) (6) Sign. ctrls Baseline Placebo $$\mathit{WB}_{i}$$ $$-$$0.074$$^{^{{ \ast \ast \ast }}}$$ $$-$$0.076$$^{^{{ \ast \ast \ast } }}$$ $$-$$0.035$$^{^{{ \ast \ast \ast }}}$$ $$-$$0.028$$^{^{{ \ast \ast \ast }}}$$ $$-$$0.028$$^{^{{ \ast \ast }}}$$ 0.006 (0.013) (0.010) (0.006) (0.006) (0.007) (0.007) Firm controls (1) No No Yes Yes Yes Yes Firm controls (2) No No No Yes Yes Yes Municipality fixed effects Yes – – – – – Industry fixed effects Yes – – – – – Industry × municipality fixed effects No Yes Yes Yes Yes Yes Main bank fixed effects No No No No Yes No $${ R}^{2}$$ 0.046 0.150 0.155 0.177 0.179 0.203 No. obs. 149,458 149,458 149,458 149,458 149,458 112,933 (1) (2) (3) (4) (5) (6) Sign. ctrls Baseline Placebo $$\mathit{WB}_{i}$$ $$-$$0.074$$^{^{{ \ast \ast \ast }}}$$ $$-$$0.076$$^{^{{ \ast \ast \ast } }}$$ $$-$$0.035$$^{^{{ \ast \ast \ast }}}$$ $$-$$0.028$$^{^{{ \ast \ast \ast }}}$$ $$-$$0.028$$^{^{{ \ast \ast }}}$$ 0.006 (0.013) (0.010) (0.006) (0.006) (0.007) (0.007) Firm controls (1) No No Yes Yes Yes Yes Firm controls (2) No No No Yes Yes Yes Municipality fixed effects Yes – – – – – Industry fixed effects Yes – – – – – Industry × municipality fixed effects No Yes Yes Yes Yes Yes Main bank fixed effects No No No No Yes No $${ R}^{2}$$ 0.046 0.150 0.155 0.177 0.179 0.203 No. obs. 149,458 149,458 149,458 149,458 149,458 112,933 Notes: OLS estimates for 2010, except for column (6), which is dated in 2006. Control variables: see Table 2. “Yes/no/–” indicates whether the corresponding set of variables is either included, not included, or redundant. In column (3) only performance-related firm control variables are included. Robust standard errors corrected for multiclustering at the industry, municipality, and main bank levels appear between parentheses. Significance levels: **$${p} < $$ 0.05, ***$${p} <$$ 0.01. View Large If we only include industry and municipality fixed effects, we obtain that employment in firms attached to weak banks falls by 7.4 pp relative to employment in unattached firms, while allowing for differential trends at the industry times municipality level leads to a treatment effect of −7.6 pp (columns 1 and 2). Next, including the only three firm-level controls that are significant according to the normalized difference test—namely capitalization, bank debt, and the number of banks—reduces the treatment effect to 3.5 pp, whereas adding all remaining firm controls brings down the effect marginally to −2.8 pp (columns 3 and 4), with half of the difference being due to the inclusion of the next two variables with the largest normalized difference, i.e., liquidity and number of past loan applications (not shown). Thus, although the estimate in column (3) is significantly different from the one obtained without any controls (column 2), further including the remaining 14 control variables does not yield a statistically different estimate. Finally, including main bank fixed effects does not alter the results (column 5), which is further proof that our weak-bank indicator captures the relevant dimensions that explain the reduced access to credit for treated firms. We therefore adopt the specification in column (4) as our baseline. Our identification relies on the assumption of parallel pre-crisis trends for treated and control firms. The validity of this assumption is tested by running a placebo regression with 2002 as the pre-crisis year and 2006 as the post-crisis year. As required, this specification test delivers a coefficient that is not significantly different from zero (column 6).19 Further evidence is provided in Figure 5. It depicts the estimated coefficients of WBi and the confidence intervals for the period 2002–2010, and it shows that the treatment effect is significantly negative from 2008 onwards. Before that time, weak-bank attachment does not produce significant differences in employment in firms in the treatment and control groups. Hence, the timing of the real effects coincides with the timing of the credit constraints at the local level (Figure 4a). Credit rationing at the firm level also follows the same pattern (Figure 4b), but these effects are less precisely estimated, which helps to explain why the treatment effect at the firm level does not become significant until 2009. Figure 5. View largeDownload slide Employment effect of weak-bank attachment, 2002–2010 (pp). Source: Authors’ computations using the data set. Figure 5. View largeDownload slide Employment effect of weak-bank attachment, 2002–2010 (pp). Source: Authors’ computations using the data set. The coincidence between the timing of the changes in credit supply and employment is reassuring, but not sufficient to establish a causal relationship. We need to demonstrate that the reductions in credit supply drive the differential evolution of employment at the firm level. Moreover, it would be incorrect to limit the analysis to a year-to-year comparison between the extent of credit rationing and the size of the employment adjustment. When the crisis erupted—and in particular after the fall of Lehman Brothers in September 2008—expectations about access to credit changed dramatically and firms in the treatment group may have rationally anticipated a further tightening of credit conditions in later years. To some extent, real effects may therefore be observed before actual credit rationing shows up in the data. Indeed, in a survey of banks undertaken by the ECB, the net balance of banks expecting an increase in the supply of credit to nonfinancial firms and banks expecting a decrease went from roughly zero in 2007Q2 to −40% already in 2007Q4, remaining there for the subsequent four quarters (Martínez-Pagés 2009). A similar survey of firms was launched by the Bank of Spain in March 2009 (Banco de España 2009). When asked about their ability to obtain funding from banks over the preceding 6 months, 40% of firms with up to 50 employees—which are the majority in our sample—reported that funding was obtained only in part or from credit institutions other than their usual ones, and 30% reported that they could not obtain any bank credit. In these two groups of firms, 65% reported that the main reason for not obtaining the funding was a change in attitude of credit institutions. Taking due account of the above observations, we now proceed with a formal test of the direct link between access to credit and changes in employment at the firm level using an IV setup that spans our entire sample period 2006–2010. 7.2. The Credit Channel We now decompose the estimated effect of the credit supply shock into two parts: the impact of weak-bank attachment on the amount of credit obtained by firms, i.e., a credit volume effect, and the pass-through of this measure of the credit shock to employment, using the following IV model: \begin{align} \Delta _{\tau }\log ( 1+n_{ij}) &=\sigma +\phi \Delta _{\tau }\log ( 1+ \mathit{Credit}_{ij}) +X_{i}^{\prime }\xi +\delta _{j}+\varepsilon _{ij} \nonumber \\ \Delta _{\tau }\log ( 1+ \mathit{Credit}_{ij}) &=\rho +\mu WB_{i}+X_{i}^{\prime }\eta +\delta _{j}+v_{ij}, \end{align} (4) in which WBi acts as an instrument for access to credit and the first stage coincides with equation (2). Therefore, μ captures the differential impact of weak-bank attachment on committed credit, whereas ϕ captures the pass-through from credit to employment. Thus, the product μϕ is equivalent to parameter β in equation (3). The exclusion restriction is that working with a weak bank alters employment growth only through credit. Although the difference between the average interest rate charged by weak and healthy banks is quite small, it is nonzero and higher for weak banks. The presence of an interest rate response, albeit small, would contradict the exclusion restriction, and as a result our second stage coefficient should be interpreted as an upper limit. Table 6 reports the estimates. The first stage coincides with our equation for credit rationing at the firm level. For the entire sample of firms, it delivers a differential drop in credit due to weak-bank attachment of 5.3 pp, while the elasticity of employment with respect to credit is estimated at 0.519 (column 1), i.e. that the elasticity of employment to the volume of credit is about one-half. This yields a compound effect on employment of −2.8 pp, which coincides with the baseline of the previous section. Next, for multibank firms we obtain a smaller impact of WBi on credit growth, −3.1 pp, but interestingly the pass-through is estimated to be larger than in the full sample, 0.797, yielding an overall impact of −2.5 pp (column 2). The estimates are highly significant and the F-statistics confirm the absence of a weak instrument problem. Table 6. The employment effect of weak-bank attachment. Instrumental variables. Dependent variable: Δ4log (1 + nij). (1) (2) All firms Multibank firms Instrumented variable $${ \Delta }_{4}\log { (1+ \mathit{Credit}}_{ijk}{ )}$$ 0.519$$^{^{{ \ast \ast \ast }}}$$ 0.797$$^{^{{ \ast \ast \ast }}}$$ (0.179) (0.294) First stage $$\mathit{WB}_{i}$$ $$-$$0.053$$^{^{{ \ast \ast \ast }}}$$ $$-$$0.031$$^{^{{ \ast \ast \ast }}}$$ (0.015) (0.011) Firm controls Yes Yes Industry × Municipality fixed effects Yes Yes Overall effect (μϕ) $$-$$0.028 $$-$$0.025 F test/p-value 13.1/0.00 7.65/0.00 No. obs. 149,458 74,045 (1) (2) All firms Multibank firms Instrumented variable $${ \Delta }_{4}\log { (1+ \mathit{Credit}}_{ijk}{ )}$$ 0.519$$^{^{{ \ast \ast \ast }}}$$ 0.797$$^{^{{ \ast \ast \ast }}}$$ (0.179) (0.294) First stage $$\mathit{WB}_{i}$$ $$-$$0.053$$^{^{{ \ast \ast \ast }}}$$ $$-$$0.031$$^{^{{ \ast \ast \ast }}}$$ (0.015) (0.011) Firm controls Yes Yes Industry × Municipality fixed effects Yes Yes Overall effect (μϕ) $$-$$0.028 $$-$$0.025 F test/p-value 13.1/0.00 7.65/0.00 No. obs. 149,458 74,045 Notes: Instrumental variable estimates for 2010. Control variables: see Table 2. Robust standard errors corrected for multiclustering at the industry, municipality, and main bank levels appear between parentheses. Significance level: ***$${p} <$$ 0.01. View Large Table 6. The employment effect of weak-bank attachment. Instrumental variables. Dependent variable: Δ4log (1 + nij). (1) (2) All firms Multibank firms Instrumented variable $${ \Delta }_{4}\log { (1+ \mathit{Credit}}_{ijk}{ )}$$ 0.519$$^{^{{ \ast \ast \ast }}}$$ 0.797$$^{^{{ \ast \ast \ast }}}$$ (0.179) (0.294) First stage $$\mathit{WB}_{i}$$ $$-$$0.053$$^{^{{ \ast \ast \ast }}}$$ $$-$$0.031$$^{^{{ \ast \ast \ast }}}$$ (0.015) (0.011) Firm controls Yes Yes Industry × Municipality fixed effects Yes Yes Overall effect (μϕ) $$-$$0.028 $$-$$0.025 F test/p-value 13.1/0.00 7.65/0.00 No. obs. 149,458 74,045 (1) (2) All firms Multibank firms Instrumented variable $${ \Delta }_{4}\log { (1+ \mathit{Credit}}_{ijk}{ )}$$ 0.519$$^{^{{ \ast \ast \ast }}}$$ 0.797$$^{^{{ \ast \ast \ast }}}$$ (0.179) (0.294) First stage $$\mathit{WB}_{i}$$ $$-$$0.053$$^{^{{ \ast \ast \ast }}}$$ $$-$$0.031$$^{^{{ \ast \ast \ast }}}$$ (0.015) (0.011) Firm controls Yes Yes Industry × Municipality fixed effects Yes Yes Overall effect (μϕ) $$-$$0.028 $$-$$0.025 F test/p-value 13.1/0.00 7.65/0.00 No. obs. 149,458 74,045 Notes: Instrumental variable estimates for 2010. Control variables: see Table 2. Robust standard errors corrected for multiclustering at the industry, municipality, and main bank levels appear between parentheses. Significance level: ***$${p} <$$ 0.01. View Large In comparison, Cingano, Manaresi, and Sette (2016), who explore the effects of the 2007 liquidity drought in interbank markets on Italian firms, find that a 10 pp reduction in credit growth reduces employment by 1.4 pp, whereas the equivalent figure in our case would be 5.2 pp, indicating a much higher elasticity than theirs. 7.3. Alternative Specifications In this section, we perform a wide range of specification tests to check the robustness of our results. We start by considering their sensitivity to alternative definitions of the treatment variable. So far, we have used a discrete treatment measure and the threshold for assignment to the treatment group was set at the first quartile of the distribution of the weak-bank loan-to-asset ratio. In our first exercise, we replace the treatment dummy by the ratio itself, which allows the intensity of credit constraints to depend on the normalized size of firms’ debt with weak banks in 2006. The corresponding coefficient, reported in the first column of Table 7, is −9.2 pp. Evaluated at the average ratio (22.8%), this delivers an overall effect of −2.1 pp. Then, we report the estimates when the threshold for our discrete treatment measure is set, respectively, at the median and the third quartile of the distribution. As we raise the threshold, the estimated treatment effect becomes stronger, going from −3.0 pp to −3.3 pp (columns 2 and 3). Neither of these estimates is statistically different from our baseline, but this exercise reveals that the magnitude of the impact increases with the degree of exposure, indicating that our choice of the first quartile as the threshold is quite conservative. Table 7. The employment effect of weak-bank attachment. Difference in Differences. Dependent variable: Δ4log (1 + nij) (1) (2) (3) (4) (5) (6) (7) (8) (9) WB Intensity Median Third quartile Survivors Alternative measure Tradable goods Loans to REI 2007 ex-ante 2002 WBi −0.092*** −0.030*** −0.033*** −0.014*** −0.034*** −0.058*** −0.030*** −0.019*** −0.015** (0.020) (0.008) (0.008) (0.004) (0.004) (0.023) (0.008) (0.006) (0.006) Firm controls yes yes yes yes yes yes yes yes yes Industry × Municipality fixed effects yes yes yes yes yes yes yes yes yes R2 0.177 0.177 0.177 0.181 0.183 0.200 0.177 0.130 0.188 No. obs. 149,458 149,458 149,458 133,122 149,458 16,199 149,458 145,322 71,703 (1) (2) (3) (4) (5) (6) (7) (8) (9) WB Intensity Median Third quartile Survivors Alternative measure Tradable goods Loans to REI 2007 ex-ante 2002 WBi −0.092*** −0.030*** −0.033*** −0.014*** −0.034*** −0.058*** −0.030*** −0.019*** −0.015** (0.020) (0.008) (0.008) (0.004) (0.004) (0.023) (0.008) (0.006) (0.006) Firm controls yes yes yes yes yes yes yes yes yes Industry × Municipality fixed effects yes yes yes yes yes yes yes yes yes R2 0.177 0.177 0.177 0.181 0.183 0.200 0.177 0.130 0.188 No. obs. 149,458 149,458 149,458 133,122 149,458 16,199 149,458 145,322 71,703 Notes. OLS estimates for 2010. Control variables: see Table 2. Robust standard errors corrected for multiclustering at the industry, municipality, and main bank levels appear between parentheses. Significance level: **p <0.05, ***p <0.01. View Large Table 7. The employment effect of weak-bank attachment. Difference in Differences. Dependent variable: Δ4log (1 + nij) (1) (2) (3) (4) (5) (6) (7) (8) (9) WB Intensity Median Third quartile Survivors Alternative measure Tradable goods Loans to REI 2007 ex-ante 2002 WBi −0.092*** −0.030*** −0.033*** −0.014*** −0.034*** −0.058*** −0.030*** −0.019*** −0.015** (0.020) (0.008) (0.008) (0.004) (0.004) (0.023) (0.008) (0.006) (0.006) Firm controls yes yes yes yes yes yes yes yes yes Industry × Municipality fixed effects yes yes yes yes yes yes yes yes yes R2 0.177 0.177 0.177 0.181 0.183 0.200 0.177 0.130 0.188 No. obs. 149,458 149,458 149,458 133,122 149,458 16,199 149,458 145,322 71,703 (1) (2) (3) (4) (5) (6) (7) (8) (9) WB Intensity Median Third quartile Survivors Alternative measure Tradable goods Loans to REI 2007 ex-ante 2002 WBi −0.092*** −0.030*** −0.033*** −0.014*** −0.034*** −0.058*** −0.030*** −0.019*** −0.015** (0.020) (0.008) (0.008) (0.004) (0.004) (0.023) (0.008) (0.006) (0.006) Firm controls yes yes yes yes yes yes yes yes yes Industry × Municipality fixed effects yes yes yes yes yes yes yes yes yes R2 0.177 0.177 0.177 0.181 0.183 0.200 0.177 0.130 0.188 No. obs. 149,458 149,458 149,458 133,122 149,458 16,199 149,458 145,322 71,703 Notes. OLS estimates for 2010. Control variables: see Table 2. Robust standard errors corrected for multiclustering at the industry, municipality, and main bank levels appear between parentheses. Significance level: **p <0.05, ***p <0.01. View Large The aim of the next exercise is to separate employment adjustments along the intensive and the extensive margins. Restricting the sample to surviving firms, the estimated treatment effect drops to −1.4 pp, which is exactly half the size of our baseline estimate (column 4). A further robustness check is to use a different definition of the dependent variable that also allows us to account for both exit and entry, originally proposed by Davis, Haltiwanger, and Schuh (1996) to study establishment-level data, namely (nijt − nijt − 1)/(0.5(nijt + nijt − 1)). The associated coefficient is −3.4 pp, which is larger but not statistically different from our baseline estimate (column 5). We now consider alternative procedures to control for local demand effects. Mian and Sufi (2014) argue that local demand effects should only affect output in nontraded goods sectors, whereas credit supply shocks should affect traded good sectors as well. We therefore aim at filtering out local demand effects by restricting attention to traded sectors. Mian and Sufi (2014) use two classifications, based on either ad hoc tradability criteria or geographical concentration. We choose the latter, because more concentrated industries are likely to be more traded and hence less dependent on local demand conditions.20 We follow these authors in computing the Herfindahl concentration index for 3-digit industries and 50 provinces, and label as tradable the goods in the highest quartile. This sample selection yields an effect on employment of −5.8 pp (column 8). It is statistically different from our baseline estimate, presumably because these firms sell in a wider geographical area and may therefore rely more on bank credit or be more sensitive to changes in credit supply, or be more sensitive to the cycle, or a combination of these factors. For our purposes, what matters is that these estimates are not the result of local demand shocks. We next check the impact of the alternative definition of weak bank, already used in Section 6.1, where weak banks are defined as those in the upper quartile of the distribution of exposure to the REI. For this definition, the measured impact is equal to −3.0 pp, which is again very similar to our baseline (column 7). In the two final checks we alter the reference period. First, we redefine the precrisis year to 2007. This choice is motivated by the fact that aggregate employment in Spain kept growing until the third quarter of 2007. Surprisingly, the estimated weak-bank effect drops to −1.9 pp (column 8). This result suggests that the slowdown in 2007 altered the mix of employment in financially vulnerable and resilient firms in the treatment and control groups, though once again this estimate does not differ statistically from the baseline. Lastly, we measure weak-bank attachment and all other variables in 2002 (column 9). Hence, firms in this sample are at least 5 years old at the start of the crisis. The table shows that the treatment effect survives, though at −1.5 pp it is significantly smaller than for the 2006 sample, suggesting that older firms were less affected by the credit supply shock, which will be confirmed in Section 9. 8. Selection Our baseline specification includes an exhaustive set of controls for observable firm characteristics, many of which moreover do not significantly differ across exposed and nonexposed firms. However, this does not completely rule out the possibility of selection effects. Our list of firm controls may still be incomplete and our estimation strategy does preclude selection on unobservables. Selection on unobservables would not be a concern if the same unobservables that are relevant for credit demand fully captured the unobservable demand effects relevant for employment growth during the crisis. There are however no strong reasons to believe that this should hold. For example, firms facing a low product demand may demand less credit to the extent that they need to produce less; however, they may also have higher demand for credit because they have lower cash flow and may need more resources to pay back outstanding liabilities. Given the importance of the selection effects, we devote Section 8.1 this issue. We can informally check the sensitivity of our estimates to the inclusion of the observable controls, so as to derive bounds for the possible bias arising from unobservable variables, as in Oster (2017). If the value of the regression R2 increases when the controls are included but the coefficient of interest does not vary much, then it is expected that the inclusion of unobservables would not alter it either. We compute a bias-adjusted estimated coefficient, following Oster (2017) in making the heuristic assumption that the maximum R2 would be 30% higher than the R2 that would be obtained if all potential determinants were included. The estimate of the effect of WBi is equal to −1.1 pp, which places a lower bound on the effect of interest. More formally, we now perform three further tests to corroborate our claim that the differential evolution of firm-level employment is not driven by selection. 8.1. Panel Estimates Our DD model is based on a cross-section and cannot therefore include firm fixed effects. To rule out the differential evolution of employment being driven by unobservable characteristics, we estimate the following panel fixed effects model (Wooldridge 2010): \begin{equation} \Delta \log (1+n_{ijt})=\alpha _{i}^{\prime }+WB_{i}^{\prime }d_{t}\beta ^{\prime }+X_{i}^{\prime }d_{t}\gamma ^{\prime }+d_{t}\delta _{j}+d_{t}\psi +v_{ijt}, \end{equation} (5) where $$\alpha _{i}^{\prime }$$ is a set of firm fixed effects, dt a vector of time dummies for t = 2007, …, 2010, and vijt a random shock. The rest of the variables are defined as before. This model includes industry times municipality times year fixed effects and both the treatment dummy and the vector of time-invariant firm characteristics are interacted with year dummies. The equivalent of β in equation (3) is the element of the coefficient vector β΄ corresponding to 2010—whose value is relative to 2007. As reported in Table 8, in this panel fixed effects specification the treatment effect amounts to −2.7, which is indistinguishable from the baseline. Interestingly, the treatment effect is statistically significant in 2008 and monotonically increasing in absolute value over time. These estimates indicate that unobservables do not play a significant role in the transmission of the credit supply shock once we filter out any trends at the industry–municipality level and across firms with different observable characteristics. Table 8. The employment effect of weak-bank attachment. Panel estimates. Dependent variable: $${ \Delta }_{4}\log ( { 1+n}_{ijt})$$. $${ 2008\times WB}_{i}$$ $$-$$0.012$$^{^{{ \ast \ast \ast }}}$$ (0.004) $${ 2009\times WB}_{i}$$ $$-$$0.020$$^{^{{ \ast \ast \ast }}}$$ (0.004) $${ 2010\times WB}_{i}$$ $$-$$0.027$$^{^{{ \ast \ast \ast }}}$$ (0.006) Firm controls Yes Firm fixed effects Yes Industry × Municipality × Year fixed effects Yes $${ R}^{2}$$ 0.789 No. obs. 563,189 $${ 2008\times WB}_{i}$$ $$-$$0.012$$^{^{{ \ast \ast \ast }}}$$ (0.004) $${ 2009\times WB}_{i}$$ $$-$$0.020$$^{^{{ \ast \ast \ast }}}$$ (0.004) $${ 2010\times WB}_{i}$$ $$-$$0.027$$^{^{{ \ast \ast \ast }}}$$ (0.006) Firm controls Yes Firm fixed effects Yes Industry × Municipality × Year fixed effects Yes $${ R}^{2}$$ 0.789 No. obs. 563,189 Notes: OLS estimates for 2007–2010. Control variables: see Table 2. Robust standard errors corrected for multiclustering at the industry, municipality, and main bank levels appear between parentheses. Significance level: ***$${p} <$$ 0.01. View Large Table 8. The employment effect of weak-bank attachment. Panel estimates. Dependent variable: $${ \Delta }_{4}\log ( { 1+n}_{ijt})$$. $${ 2008\times WB}_{i}$$ $$-$$0.012$$^{^{{ \ast \ast \ast }}}$$ (0.004) $${ 2009\times WB}_{i}$$ $$-$$0.020$$^{^{{ \ast \ast \ast }}}$$ (0.004) $${ 2010\times WB}_{i}$$ $$-$$0.027$$^{^{{ \ast \ast \ast }}}$$ (0.006) Firm controls Yes Firm fixed effects Yes Industry × Municipality × Year fixed effects Yes $${ R}^{2}$$ 0.789 No. obs. 563,189 $${ 2008\times WB}_{i}$$ $$-$$0.012$$^{^{{ \ast \ast \ast }}}$$ (0.004) $${ 2009\times WB}_{i}$$ $$-$$0.020$$^{^{{ \ast \ast \ast }}}$$ (0.004) $${ 2010\times WB}_{i}$$ $$-$$0.027$$^{^{{ \ast \ast \ast }}}$$ (0.006) Firm controls Yes Firm fixed effects Yes Industry × Municipality × Year fixed effects Yes $${ R}^{2}$$ 0.789 No. obs. 563,189 Notes: OLS estimates for 2007–2010. Control variables: see Table 2. Robust standard errors corrected for multiclustering at the industry, municipality, and main bank levels appear between parentheses. Significance level: ***$${p} <$$ 0.01. View Large 8.2. Matching Estimates We have already pointed out the presence of some degree of heterogeneity between treated and control firms. Matching techniques allow us to directly compare similar firms in both groups. This avoids problems derived from a possible lack of overlap between the characteristics of firms in the two groups, and it improves the efficiency of our estimates. For the sake of completeness, we use both propensity score and exact matching for our discrete and continuous treatment variables, thus obtaining four different estimates. The propensity score matching estimates are derived from first estimating a probit model for the probability that a firm borrows from a weak bank—which includes the same controls as the baseline regression—and then estimating our baseline model using the weights coming from the sample balanced on all the observables used for the propensity score. In exact matching, we compare treated and nontreated firms within industry times municipality and firm control cells. For the latter, we use the coarsened exact matching method (Iacus, King, and Porro 2011), where all characteristics are entered as 0–1 dummy variables (see Appendix B for details). We end up with 6,556 strata with observations that can be matched across treated and control firms, out of a total of 13,520 strata, so that only 2,122 firms (5.1%) in the treatment group are left without a matching control firm, and the treatment effect is estimated using the method of weighted least squares. Table 9 reports the results. For the discrete treatment measure WBi, the estimated effects with propensity score and exact matching are, respectively, −3.2 pp and −1.6 pp (columns 1 and 2).21 With the continuous measure, the corresponding coefficients are −6.5 pp and −5.2 pp. Because average exposure among attached firms is 22.8%, the average treatment effects are, respectively, −1.5 pp and −1.2 pp (columns 3 and 4). Thus, in both cases, propensity score matching delivers larger effects and, in line with our previous results, the continuous measure implies somewhat lower effects than the discrete treatment dummy. Importantly, all four estimates are significantly different from zero and they lie within the confidence intervals of their respective baseline estimates. Table 9. The employment effect of weak-bank attachment. Matching. Dependent variable: $${ \Delta }_{4}\log ( { 1+n}_{ijt})$$. (1) (2) (3) (4) Propensity score Exact Propensity score Exact $$\mathit{WB}_{i}$$ $$-$$0.032$$^{^{{ \ast \ast \ast }}}$$ $$-$$0.016$$^{^{{ \ast \ast }}}$$ (0.009) (0.009) $$\mathit{WB}_{i}$$$${\mathit {Intensity}}$$ $$-$$0.065$$^{^{{ \ast \ast \ast }}}$$ $$-$$0.052$$^{^{{ \ast \ast }}}$$ (0.016) (0.020) Firm controls Yes Yes Yes Yes Industry × municipality fixed effects Yes Yes Yes Yes Overall effect – – $$-$$0.016 $$-$$0.012 $${ R}^{2}$$ 0.228 0.245 0.228 0.245 No. obs. 55,712 133,816 55,712 133,816 (1) (2) (3) (4) Propensity score Exact Propensity score Exact $$\mathit{WB}_{i}$$ $$-$$0.032$$^{^{{ \ast \ast \ast }}}$$ $$-$$0.016$$^{^{{ \ast \ast }}}$$ (0.009) (0.009) $$\mathit{WB}_{i}$$$${\mathit {Intensity}}$$ $$-$$0.065$$^{^{{ \ast \ast \ast }}}$$ $$-$$0.052$$^{^{{ \ast \ast }}}$$ (0.016) (0.020) Firm controls Yes Yes Yes Yes Industry × municipality fixed effects Yes Yes Yes Yes Overall effect – – $$-$$0.016 $$-$$0.012 $${ R}^{2}$$ 0.228 0.245 0.228 0.245 No. obs. 55,712 133,816 55,712 133,816 Notes: Weighted least squares estimates for 2010. Control variables: see Table 2. Robust standard errors corrected for multiclustering at the industry, municipality, and main bank levels appear between parentheses. Significance levels: **$${p} <$$ 0.05, ***$${p} <$$ 0.01. View Large Table 9. The employment effect of weak-bank attachment. Matching. Dependent variable: $${ \Delta }_{4}\log ( { 1+n}_{ijt})$$. (1) (2) (3) (4) Propensity score Exact Propensity score Exact $$\mathit{WB}_{i}$$ $$-$$0.032$$^{^{{ \ast \ast \ast }}}$$ $$-$$0.016$$^{^{{ \ast \ast }}}$$ (0.009) (0.009) $$\mathit{WB}_{i}$$$${\mathit {Intensity}}$$ $$-$$0.065$$^{^{{ \ast \ast \ast }}}$$ $$-$$0.052$$^{^{{ \ast \ast }}}$$ (0.016) (0.020) Firm controls Yes Yes Yes Yes Industry × municipality fixed effects Yes Yes Yes Yes Overall effect – – $$-$$0.016 $$-$$0.012 $${ R}^{2}$$ 0.228 0.245 0.228 0.245 No. obs. 55,712 133,816 55,712 133,816 (1) (2) (3) (4) Propensity score Exact Propensity score Exact $$\mathit{WB}_{i}$$ $$-$$0.032$$^{^{{ \ast \ast \ast }}}$$ $$-$$0.016$$^{^{{ \ast \ast }}}$$ (0.009) (0.009) $$\mathit{WB}_{i}$$$${\mathit {Intensity}}$$ $$-$$0.065$$^{^{{ \ast \ast \ast }}}$$ $$-$$0.052$$^{^{{ \ast \ast }}}$$ (0.016) (0.020) Firm controls Yes Yes Yes Yes Industry × municipality fixed effects Yes Yes Yes Yes Overall effect – – $$-$$0.016 $$-$$0.012 $${ R}^{2}$$ 0.228 0.245 0.228 0.245 No. obs. 55,712 133,816 55,712 133,816 Notes: Weighted least squares estimates for 2010. Control variables: see Table 2. Robust standard errors corrected for multiclustering at the industry, municipality, and main bank levels appear between parentheses. Significance levels: **$${p} <$$ 0.05, ***$${p} <$$ 0.01. View Large Table 10. Descriptive statistics of firms below (control) and above (treated) the median of the weak-bank density ratio in 1988 (2006). Control Treated Mean St. dev. P25 P50 P75 Mean St. dev. P25 P50 P75 Normalized differences Loans with WB/assets 4.8 11.9 0.0 0.0 2.1 8.8 15.1 0.0 0.0 11.8 0.20 Share of loans with WB 19.3 34.2 0.0 0.0 24.2 32.3 39.8 0.0 5.0 67.8 0.25 Employment (employees) 29.5 375.3 2.0 6.0 14.0 18.3 273.3 2.0 5.0 12.0 $$-$$0.02 Temporary employment 19.9 25.3 0.0 10.0 33.3 22.2 25.9 0.0 14.0 35.1 0.06 Age (years) 12.6 9.9 6.0 11.0 17.0 12.0 9.1 6.0 11.0 16.0 $$-$$0.04 Size (million euros) 6.9 132.9 0.3 0.6 1.8 3.5 52.8 0.2 0.6 1.6 $$-$$0.02 Exporter 12.6 33.1 0.0 0.0 0.0 13.6 34.2 0.0 0.0 0.0 0.02 Own funds/assets 32.6 23.2 13.3 28.2 48.3 30.6 22.5 12.1 25.9 45.2 $$-$$0.06 Liquidity/assets 11.7 14.8 1.6 6.1 16.1 11.0 13.8 1.6 5.9 15.1 $$-$$0.03 Return on assets 6.4 11.3 1.7 4.7 9.9 6.0 10.3 1.9 4.7 9.1 $$-$$0.03 Bank debt 34.3 27.2 10.0 30.4 54.6 37.4 26.8 14.0 34.6 57.6 0.08 Short-term bank debt (<1 year) 48.4 40.9 0.0 46.7 97.3 47.4 39.8 0.0 45.5 90.6 $$-$$0.02 Long-term bank debt (<5 years) 23.0 35.7 0.0 0.0 43.4 24.6 35.7 0.0 0.0 48.6 0.03 Noncollateralized bank debt 79.7 34.5 68.2 100.0 100.0 79.4 34.0 64.5 100.0 100.0 $$-$$0.01 Credit line (has one) 71.0 45.4 0.0 100.0 100.0 68.8 46.3 0.0 100.0 100.0 $$-$$0.03 Banking relationships (no.) 2.2 2.0 1.0 2.0 3.0 2.3 2.0 1.0 2.0 3.0 0.03 Current loan defaults 0.4 6.2 0.0 0.0 0.0 0.4 6.2 0.0 0.0 0.0 0.00 Past loan defaults 1.7 12.9 0.0 0.0 0.0 1.7 13.0 0.0 0.0 0.0 0.00 Past loan applications 57.2 49.5 0.0 100.00 100.00 59.8 49.0 0.0 100.0 100.0 0.04 All loan applications accepted 22.7 41.9 0.0 0.0 0.0 23.7 42.5 0.0 0.0 100.0 0.02 Control Treated Mean St. dev. P25 P50 P75 Mean St. dev. P25 P50 P75 Normalized differences Loans with WB/assets 4.8 11.9 0.0 0.0 2.1 8.8 15.1 0.0 0.0 11.8 0.20 Share of loans with WB 19.3 34.2 0.0 0.0 24.2 32.3 39.8 0.0 5.0 67.8 0.25 Employment (employees) 29.5 375.3 2.0 6.0 14.0 18.3 273.3 2.0 5.0 12.0 $$-$$0.02 Temporary employment 19.9 25.3 0.0 10.0 33.3 22.2 25.9 0.0 14.0 35.1 0.06 Age (years) 12.6 9.9 6.0 11.0 17.0 12.0 9.1 6.0 11.0 16.0 $$-$$0.04 Size (million euros) 6.9 132.9 0.3 0.6 1.8 3.5 52.8 0.2 0.6 1.6 $$-$$0.02 Exporter 12.6 33.1 0.0 0.0 0.0 13.6 34.2 0.0 0.0 0.0 0.02 Own funds/assets 32.6 23.2 13.3 28.2 48.3 30.6 22.5 12.1 25.9 45.2 $$-$$0.06 Liquidity/assets 11.7 14.8 1.6 6.1 16.1 11.0 13.8 1.6 5.9 15.1 $$-$$0.03 Return on assets 6.4 11.3 1.7 4.7 9.9 6.0 10.3 1.9 4.7 9.1 $$-$$0.03 Bank debt 34.3 27.2 10.0 30.4 54.6 37.4 26.8 14.0 34.6 57.6 0.08 Short-term bank debt (<1 year) 48.4 40.9 0.0 46.7 97.3 47.4 39.8 0.0 45.5 90.6 $$-$$0.02 Long-term bank debt (<5 years) 23.0 35.7 0.0 0.0 43.4 24.6 35.7 0.0 0.0 48.6 0.03 Noncollateralized bank debt 79.7 34.5 68.2 100.0 100.0 79.4 34.0 64.5 100.0 100.0 $$-$$0.01 Credit line (has one) 71.0 45.4 0.0 100.0 100.0 68.8 46.3 0.0 100.0 100.0 $$-$$0.03 Banking relationships (no.) 2.2 2.0 1.0 2.0 3.0 2.3 2.0 1.0 2.0 3.0 0.03 Current loan defaults 0.4 6.2 0.0 0.0 0.0 0.4 6.2 0.0 0.0 0.0 0.00 Past loan defaults 1.7 12.9 0.0 0.0 0.0 1.7 13.0 0.0 0.0 0.0 0.00 Past loan applications 57.2 49.5 0.0 100.00 100.00 59.8 49.0 0.0 100.0 100.0 0.04 All loan applications accepted 22.7 41.9 0.0 0.0 0.0 23.7 42.5 0.0 0.0 100.0 0.02 Notes: Observations—149,458 firms; 106,128 control and 43,330 treated firms. WB denotes weak banks. Variables are ratios in percentages unless otherwise indicated. The last column shows the normalized difference test of Imbens and Wooldridge (2009). See definitions in Appendix B. View Large Table 10. Descriptive statistics of firms below (control) and above (treated) the median of the weak-bank density ratio in 1988 (2006). Control Treated Mean St. dev. P25 P50 P75 Mean St. dev. P25 P50 P75 Normalized differences Loans with WB/assets 4.8 11.9 0.0 0.0 2.1 8.8 15.1 0.0 0.0 11.8 0.20 Share of loans with WB 19.3 34.2 0.0 0.0 24.2 32.3 39.8 0.0 5.0 67.8 0.25 Employment (employees) 29.5 375.3 2.0 6.0 14.0 18.3 273.3 2.0 5.0 12.0 $$-$$0.02 Temporary employment 19.9 25.3 0.0 10.0 33.3 22.2 25.9 0.0 14.0 35.1 0.06 Age (years) 12.6 9.9 6.0 11.0 17.0 12.0 9.1 6.0 11.0 16.0 $$-$$0.04 Size (million euros) 6.9 132.9 0.3 0.6 1.8 3.5 52.8 0.2 0.6 1.6 $$-$$0.02 Exporter 12.6 33.1 0.0 0.0 0.0 13.6 34.2 0.0 0.0 0.0 0.02 Own funds/assets 32.6 23.2 13.3 28.2 48.3 30.6 22.5 12.1 25.9 45.2 $$-$$0.06 Liquidity/assets 11.7 14.8 1.6 6.1 16.1 11.0 13.8 1.6 5.9 15.1 $$-$$0.03 Return on assets 6.4 11.3 1.7 4.7 9.9 6.0 10.3 1.9 4.7 9.1 $$-$$0.03 Bank debt 34.3 27.2 10.0 30.4 54.6 37.4 26.8 14.0 34.6 57.6 0.08 Short-term bank debt (<1 year) 48.4 40.9 0.0 4